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Nudges receive growing attention as an effective concept to alter people's decisions without significantly changing economic incentives or limiting options. However, being often very subtle and covert, nudges are also criticized as unethical. By not being transparent about the intention to influence individual choice they might be perceived as limiting freedom of autonomous actions and decisions. So far, empirical research on this issue is scarce. In this study, we investigate whether nudges can be made transparent without limiting their effectiveness. For this purpose we conduct a laboratory experiment where we nudge contributions to carbon emission reduction by introducing a default value. We test how different types of transparency (i.e. knowledge of the potential influence of the default, its purpose, or both) influence the effect of the default. Our findings demonstrate that the default increases contributions, and information on the potential influence, its purpose, or both combined do not significantly influence the default effect. Furthermore, we do not find evidence that psychological reactance interacts with the influence of transparency. Findings support the policy-relevant claim that nudges (in the form of defaults) can be transparent and yet effective.
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Can Nudges Be Transparent and Yet Effective?
Hendrik Brunsa,
, Elena Kantorowicz-Reznichenkob,
, Katharina Klementc,
Marijane Luistro Jonssond, Bilel Rahalie
aInternational Max-Planck Research School on Earth System Modelling; Department of
Socioeconomics, University of Hamburg, Welckerstr. 8, 20354 Hamburg, Germany
bErasmus University Rotterdam, P.O. Box 1738, 3000 DR Rotterdam, The Netherlands
cFriedrich-Schiller-University Jena
dStockholm School of Economics
eUniversit´e de Grenoble Alpes-Institut National de la Recherche Agronomique
Abstract
Nudges receive growing attention as an effective concept to alter people’s
decisions without significantly changing economic incentives or limiting op-
tions. However, being often very subtle and covert, nudges are also criticized
as unethical. By not being transparent about the intention to influence in-
dividual choice they might be perceived as limiting freedom of autonomous
actions and decisions. So far, empirical research on this issue is scarce. In this
study, we investigate whether nudges can be made transparent without limit-
ing their effectiveness. For this purpose we conduct a laboratory experiment
where we nudge contributions to carbon emission reduction by introducing
a default value. We test how different types of transparency (i.e. knowledge
of the potential influence of the default, its purpose, or both) influence the
effect of the default. Our findings demonstrate that the default increases con-
tributions, and information on the potential influence, its purpose, or both
combined do not significantly influence the default effect. Furthermore, we
do not find evidence that psychological reactance interacts with the influence
of transparency. Findings support the policy-relevant claim that nudges (in
the form of defaults) can be transparent and yet effective.
Corresponding author
©2018. This manuscript version is made available under the CC-BY-NC-ND 4.0 license
http://creativecommons.org/licenses/by-nc-nd/4.0/
Email addresses: hendrik.bruns@wiso.uni-hamburg.de (Hendrik Bruns),
reznichenko@law.eur.nl (Elena Kantorowicz-Reznichenko)
Preprint submitted to Journal of Economic Psychology February 28, 2018
Keywords: climate protection, experiment, default, nudge, transparency,
public good
JEL: D03, H41, Q58, K23
PsycINFO classficiation code: 3000, 3900, 4000, 4070
1. Introduction
Nudges, a concept coined by Thaler & Sunstein (2008), describe a diverse
set of instruments that utilize behavioral insights in order to affect individual
behavior, without limiting options or significantly changing economic incen-
tives. They have become an alternative to economic interventions. While
nudges affect behavior by changing the context, thus primarily focusing on
automatic decision processes, incentives can be seen to change cognition in-
stead, thus focusing on conscious decision making (Dolan et al., 2012). The
recent success of this approach is as a direct consequence of conceiving indi-
vidual behavior as bounded, instead of perfectly rational and selfish (Bolton
& Ockenfels, 2012). Nudges are evolving into a popular form of soft regula-
tion in various fields such as health, finance, and environmental protection
(Sunstein, 2014a; Alemanno & Sibony, 2015; World Bank, 2015; Lourenco
et al., 2016). Despite its growing popularity, the use of behavioral insights
in policy-making is subject to criticism (e.g. Hausman & Welch, 2010; Re-
bonato, 2014). One remarkable and often criticized aspect of nudges is that
they often influence individual behavior without being noticed by the af-
fected subject (Dhingra et al., 2012; Hansen & Jespersen, 2013; Sunstein,
2016). This raises the concern that nudges covertly violate individual au-
tonomy and are therefore unethical (Bovens, 2009; House of Lords Report,
2011). Such regulation thus lacks the transparency that characterizes other
regulatory instruments. For instance, when the government imposes a tax
to reduce consumption of a product (e.g. cigarettes, or carbon dioxide),
people are aware of this tax and can compel the government to justify it
(Sunstein, 2014b). On the other hand, when the government sets an opt-out
system instead of an opt-in system to promote certain behavior (e.g. or-
gan donation) it exploits several psychological biases, often without people’s
awareness (Hansen & Jespersen, 2013). Felsen et al. (2013) demonstrate in a
vignette study that a significant proportion of individuals have reservations
towards nudges they perceive as covert. Additionally, another recent research
stream provides evidence of the intrinsic value of decision rights and auton-
omy (Fehr et al., 2013; Bartling et al., 2014; Owens et al., 2014). To address
2
this criticism we investigate whether nudges can be made transparent with-
out reducing their effectiveness. In this context, we take into account that
the covert nature of nudges is often said to be essential for their effectiveness
(Bovens, 2009; House of Lords Report, 2011). Also, we acknowledge that
telling people that the nudge is used to influence their decision potentially
evokes a perceived threat to their freedom, leading them to experience psy-
chological reactance. The latter can be defined as ”the motivational state
that is hypothesized to occur when a freedom is eliminated or threatened
with elimination” (Brehm & Brehm, 2013, p. 37). This could not only in-
hibit the effect of the nudge but could even lead to the opposite effect than
the one intended. We presume that experiencing reactance is mitigated when
information on its purpose substitutes or complements the nudge. Accord-
ing to salience theory (Bordalo et al., 2012), providing the purpose increases
the degree to which the ultimate goal of the nudge, relative to its means
of behavioral influence, is taken into account during the decision process.
This hypothetically reduces the propensity to elicit a state of psychological
reactance. Therefore, this phenomenon is important when investigating the
influence of different types of transparency on the effectiveness of nudges.
We report evidence from a laboratory experiment where subjects can con-
tribute to real climate protection. The nudge is a default value that intends
to increase contributions. Such a default in a public goods context, unlike
nudges aiming to improve individual outcomes, attempts to increase positive
external effects that only benefit the individual in the aggregate, but affords
them to forfeit immediate personal economic gains.1Thus, this context is
more likely to produce a state of psychological reactance, and is thus suitable
for testing it.
In general, there are different mechanisms through which a default po-
tentially influences behavior, e.g. as a reference value and anchor (for con-
struction of preferences), through provision of social norms or information,
or through inertia (by imposing pecuniary or cognitive costs on deviating
from the default). Sunstein & Reisch (2016) provide a review on default-
mechanisms. Note that Cappelletti et al. (2014) provide evidence from a
public good game that defaults do not work as recommendations, i.e. as
1Hagman et al. (2015) divide nudges into pro-self and pro-social. While the former
nudge people towards making better decisions for themselves, the latter nudge people
towards behavior that benefits society.
3
information provision in such a context. We expect the default value to in-
crease contributions through two possible ways. First, it can increase the
fraction of people picking the default value. Second, it can induce people
to increase their contribution towards this value. We discuss our possible
mechanisms in the second section and relate them to our findings in the last
section.
The type of transparency that accompanies the default varies across treat-
ments and consists of either informing decision makers about its potential
behavioral influence and/or informing them about its purpose to increase
contributions to climate protection. After the experiment, we assess two
different measures of psychological reactance. Thus, we test whether the in-
fluence of transparency is limited to a sub-group of participants distinct in
their proneness to show psychological reactance (trait reactance). Addition-
ally, we test whether transparency influences the perception of a nudge as a
threat for freedom of choice, and whether it functions as a source of anger
(state reactance).
Recent findings from Arad & Rubinstein (2017) illustrate why our inves-
tigation of transparency and psychological reactance in the context of nudges
is important. Their findings suggest that some subjects may consciously act
contrary to the encouraged action, presumably in order to protest against the
intervention of the government. The authors argue that full transparency of
nudges, thus, may even lead to the opposite outcome than the one intended
(as opposed to simply eliminating the effectiveness of a nudge). Some peo-
ple behave in a completely different way simply out of protest against being
manipulated. Contrary to this argument, findings by Sunstein (2016) from
a nationally representative survey in the USA show that there is widespread
support for nudges, and that transparency concerning the nudge will not di-
minish its effectiveness. Reisch & Sunstein (2016) show that there is also a
general support of nudges in six European countries.
To the best of our knowledge, there are only three empirical studies di-
rectly relevant to our research question. Loewenstein et al. (2015), in a
laboratory experiment, find no evidence that informing subjects that they
were presented with a pro-self default option influences their effectiveness.
Similarly, Kroese et al. (2016), in a field experiment, find no evidence that
making subjects aware of the purpose behind a pro-self default has any ef-
fect. Steffel et al. (2016), in several hypothetical and marginally incentivized
consumer-related experiments, find no evidence that stressing the potential
behavioral influence of a pro-self, as well as a pro-social default impacts their
4
effectiveness, although it affects perception by the consumer.
While existing evidence unanimously suggests the impact of transparency
on effectiveness of nudges is absent, our research augments the extant liter-
ature in various ways. First, subjects in our experiment face a trade-off
between real monetary payoffs and real contributions to a (global) public
good. By contrast, two of the previous studies employed relatively abstract
and stylized environments, and did not demand subjects to make (substan-
tial) financial tradeoffs. Although Kroese et al. (2016) investigate behavior
in the field, they do neither study pro-social nudges, nor do they incorporate
both types of transparency. Second, we investigate the distinct, as well as
combined effect of two types of transparency on the default effect. Previous
research focused exclusively on either of these two categories. However, there
are reasons to expect that informing decision makers about the potential be-
havioral influence of a nudge has different consequences than informing them
about its purpose. Third, we enrich our analysis with the concept of psycho-
logical reactance, allowing for a deeper understanding of potential channels
through which transparency influences default effects. Recent research on
nudges, although focusing conceptually on the role of reactance (Arad & Ru-
binstein, 2017; Hedlin & Sunstein, 2016), did not investigate its interaction
with transparency.
Consequently, we contribute to the topic of transparency of nudges in
various ways. First, we enable a more nuanced view by investigating two
types of transparency, thus contributing to a better understanding on how
transparency works and whether policy-makers can make nudges more trans-
parent without diminishing effectiveness. Second, our experimental setup,
albeit controlled, sets up a realistic context, enabling us to make more valid
inferences about the impact of transparency on nudges in ”the real world”.
Third, we widen the discussion on transparency by investigating its connec-
tion to the concept of psychological reactance.
To preview our results, defaulted contributions are significantly higher
than in the control group, even when accompanied by either type of trans-
parency, including both types. In addition, contributions in the treatment
groups (with or without transparency) do not significantly differ from each
other. Thus, we replicate the lack of an effect of transparency, indicated
by evidence from the studies outlined above. Finally, we neither find evi-
dence that trait reactance interacts with transparency, nor that transparency
changes the perception of nudges as freedom threatening or sources of anger.
Therefore, our findings advocate that nudges (in the form of defaults) can
5
be transparent and effective.
The remainder of the article is structured as follows. In Section 2 we
discuss psychological reactance as a conceptual background to covert nudges,
followed by derivation of behavioral predictions. We lay out the experimental
design in Section 3. In Section 4 we present and analyze the results. Section
5 concludes.
2. Conceptual framework and behavioral predictions
Since Brehm (1966) introduced the theory of psychological reactance,
many studies have explored this phenomenon. Social influence attempts
(such as nudges) that are detected by an individual may be perceived as a
threat to freedom of choice (Brehm, 1966). The elicited state of psychological
reactance may result in behavioral and cognitive efforts to reestablish free-
dom as well as uncomfortable, hostile, aggressive, and angry feelings (Dillard
& Shen, 2005). Consequently, people may try to restore their freedom by ex-
hibiting exactly the restricted behavior, thus, in our case, strongly deviating
from the default value. In addition, they may devaluate the source of threat
(the initiator of the nudge), increase their liking for the restricted freedom,
or counter-argue against the imposed option (Brehm, 1966; Dillard & Shen,
2005). People react in such a manner not only to obvious and direct, but
also to subtle and subliminal threats (Chartrand et al., 2007).
In order to investigate whether transparency influences the effectiveness
of pro-social nudges, specifically defaults, we chose the context of climate
protection. With climate change being one of the major challenges faced by
society on a global scale today, information-based instruments and nudges
are becoming increasingly important to increase individual contributions to
climate and environmental protection (Allcott & Mullainathan, 2010; Ara˜na
& Le´on, 2013; World Bank, 2015).
One way to contribute to climate protection is to offset (parts of) one’s
own yearly CO2emissions by donating to specific charitable organizations
(in the experiment, referred to as ’climate protection fund’). These organi-
zations use donations to purchase and delete carbon emission licenses from
the European Union Emissions Trading Scheme (EU ETS).2Buying carbon
2The EU ETS is a European market that prices carbon emissions and allows regulated
industries to trade their emission rights. Buying licenses off the market increases the
scarcity of emission rights, resulting in higher prices and thus increasing the incentives for
6
licenses is an effective way for individuals to contribute to climate protection,
when compared to, e.g. electricity-saving (Perino, 2015). Therefore, individ-
ual payment for carbon license retirement is a relevant context in which the
influence of transparency on the effectiveness of a pro-social nudge can be
investigated.
Based on psychological reactance theory we expect that mentioning the
potential influence of a default will evoke the most reactance and thus re-
duce its effectiveness. In contrast, the sole provision of the purpose, i.e.
climate protection, should evoke little reactance since this induces perspec-
tive taking. In addition, it renders the positive goal of the contribution more
salient. According to salience theory formulated by Bordalo et al. (2012),
more salient attributes will be over-weighted in the decision process. Based
on this argument, providing the purpose will work as an additional nudge and
thus increase the default effect. Finally, accompanying the default with both
types of information will be the most transparent form of the nudge. Due
to combining the hypothesized ”downside” effect of reactance and ”upside”
effect of the salience of the purpose of the nudge we expect the contribution
level to be in between the other treatments. In sum, hypotheses concerning
people’s contribution decisions in the presence of the default are as follows:
H1: If participants are confronted with a default, contributions will be
higher compared to when there is no default.
H2: If participants are informed that the default may have an influence
on their decision, contributions will be lower compared to when they are not
informed.
H3: If participants are informed of the purpose of the default, contribu-
tions will be higher compared to when they are not informed.
H4: If participants are informed of the potential influence of a default
and of its purpose, contributions will be higher than with information solely
on influence and lower than with information solely on purpose.
Although it is not the purpose of this paper to identify the mechanism
regulated firms to invest in emission-reducing technology.
7
underlying the potential default effect, hypothesizing about a transparency-
effect relies on certain assumptions regarding this mechanism. Transparency
can only exert an effect if subjects are aware of the transparency and con-
sequently of the default. This necessity rules out default effects that rely on
unawareness (Madrian & Shea, 2001). If defaults work via costs of opting
out (Johnson & Goldstein, 2003), providing a reference point (Samuelson &
Zeckhauser, 1988; Dinner et al., 2011) or an anchor (Dhingra et al., 2012),
transparency could have an impact.3More precisely, information regarding
the potential influence of the default then increases the awareness of decision
makers to the manipulated structure of the decision. This in turn then may
cause reactance. Mentioning the purpose of the default and thus justifying
its use has the potential to mitigate reactance. However, note that Wilson
et al. (1996) observe anchoring effects despite forewarning, suggesting an un-
intentional and subconscious working mechanism that could also apply to
defaults working as anchors. If defaults work as an implicit recommendation
(McKenzie et al., 2006), a persuasion attempt (Brown & Krishna, 2004), or
a coordination device (Cappelletti et al., 2014) it is less clear whether trans-
parency has an effect. Informing decision makers on the potential influence
given their interpretation of the default as a recommendation, persuasion
attempt, or coordination device would provide no additional information,
because decision makers would already be aware of this potential influence.
Mentioning the purpose would increase the salience of the climate protection
goal, causing a similar effect as when any of the previous mechanisms is at
play.
When analyzing findings with respect to psychological reactance, we hy-
pothesize that trait reactance interacts with the type of transparency accom-
panying the default value. Specifically, we expect that:
H5: If participants are informed that the default may have an influence
on their decision, the default effect for participants with higher trait reac-
tance will be lower than for participants with lower trait reactance.
We further hypothesize that the evaluation of a default as freedom-threatening,
3Note that the potential impact can vary considerably between these mechanisms, and
that it can also be close to zero. The point is that here, as opposed to the case of
unawareness, transparency could logically influence the default effect.
8
autonomy-decreasing, manipulative, and pressuring (perceived threat to free-
dom), as well as its potential to elicit negative emotions (anger) differs with
respect to the types of transparency accompanying the default value. Specif-
ically, we expect that:
H6: If participants are informed that the default may have an influence
on their decision, experience of state reactance will be higher compared to
when they are not informed.
We deduce hypotheses H5 and H6 exclusively with respect to a default ac-
companied by information on its potential influence, because we expect this
type of transparency to increase the salience of the potentially manipulative
and autonomy-threatening default-characteristic. For the purpose of the de-
fault, the conceptual link to reactance is less clear. We therefore abstain
from formulating specific hypotheses.
3. Experimental design
The laboratory experiment consisted of five experimental groups, of which
one was the control group.4We conducted 11 sessions in the Econ-lab of
the Erasmus School of Economics at the Erasmus University Rotterdam,
the Netherlands, recruited with ORSEE in June 2016, and additional 15
sessions in July 2017 in the WiSo-lab of the University of Hamburg, Germany,
recruited with hroot (Bock et al., 2014). A total of 498 students participated
in the experiment using the z-tree software (Fischbacher, 2007). Of these,
53.21% were female, the average age was 23.74 years (median: 23 years), and
about half (53.01%) studied economics. More information on the differences
between samples from both locations, as well as a disaggregated analysis of
effect-differences are provided in Appendix B.1.
All participants were randomly assigned to separate computer terminals
and were instructed not to communicate. They were given instruction sheets
4Prior to the experiment, pilot sessions were conducted in Germany (n= 16), Sweden
(n= 25), France (n= 29) and The Netherlands (n= 32). The pilot session in Germany
focused on developing the design, which was further improved on and tested among Master
students in the Netherlands, Sweden, and Bachelor students in France. The experimental
design was not identical in all these pilots. Therefore, findings these sessions are not
included in the data analysis.
9
that were read aloud (see Appendix A). All participants received an en-
dowment of 10 Euro and were asked to indicate how much (if any) of their
endowment they would like to contribute to the ’climate protection fund’.
The remaining amount was their private payoff. After the experiment, they
were paid according to their decisions, and contributions were used to retire
real carbon licenses from the EU ETS, through donations to ’TheCompen-
sators*’.5
In the control group, participants were presented with a text box where
they could enter their contribution in any integer amount between 0 and
10 Euro. Neither a preselected default value for the contribution, nor any
additional information were presented. In the other experimental groups,
subjects encountered an 8 Euro default contribution in form of a button (see
Figures A.2 - A.3 in Appendix A). They could either press this button or
choose another one that stated ’Different amount’. In the latter case they
were referred to another screen that contained exactly the same information
but with the addition of a text box where they could insert any amount be-
tween 0 and 10 Euro. In three of four default treatments, the default was
complemented by a sentence that induced transparency, respectively on the
default’s potential influence, its purpose, or both. Table 1 shows the exact
wording used to provide each type of transparency in the respective treat-
ment group.
[Table 1 about here]
The Default+Info transparency message informs subjects about the fact that
they may be (subconsciously) affected by the default value. It resembles the
wording by Steffel et al. (2016) which they use in order to deploy a default
ethically. We expect that this wording stimulates the participants defensive
systems against the threat to their behavioral autonomy, potentially motivat-
ing reactant behavior. The Default+Purpose transparency message informs
subjects about the purpose of the default, i.e. increasing contributions to
the climate protection fund. The wording implies the existence of a default
effect, increases the salience of the purpose and, contrary to Default+Info,
5’TheCompensators*’ is a non-profit association founded in 2006 by researchers from
the Potsdam Institute for Climate Impact Research. They offer a way for individuals and
firms to compensate for their emissions. With donations, they buy and retire emission
rights from the EU ETS. At the end of the experiment, all participants received an email
with a confirmation and a certificate of aggregate experimental donations to ’TheCom-
pensators*’.
10
causes subjects to focus on the goal instead of the fact that it potentially
threatens their behavioral autonomy. The Default+Info+Purpose combines
both messages. Once subjects made their decision, they received information
regarding their contribution, their private payoff and the amount of CO2that
would be retired with the contributed amount.6
After making their decision, participants answered a questionnaire mea-
suring, among others, their attributed importance to climate protection, and
their belief in the effectiveness of retiring emission rights as a measure to
protect the climate. In order to find out whether reactions to the different
types of transparency can be explained by psychological reactance, we have
two approaches. First, we assess participants’ perception of the default value
as freedom threatening, autonomy-decreasing, manipulative, and pressuring,
as well as its tendency to evoke negative emotional reactions, such as irrita-
tion, anger, annoyance, and aggravation. We refer to this as state reactance
(Dillard & Shen, 2005). Second, we measure subjects’ proneness to psycho-
logical reactance, referred to as trait reactance, with Hong’s Psychological
Reactance Scale (Hong & Faedda, 1996). Both measures were assessed after
subjects made their decision of how much to contribute.7Relevant questions
are in Appendix C.
After conducting the sessions in Rotterdam, we calculated observed power
for the most important tests. For H1, simulated post-hoc observed power
analyses produced power coefficients of 0.72, 0.26, 0.51, and 0.46, respec-
tively for Control vs. Default, Control vs. Default+Information, Control
vs. Default+Purpose, and Control vs. Default+Info+Purpose. Concern-
ing Findings 2-4, post-hoc observed power analyses for the estimates in
model (1) produced power coefficients of 0.22, 0.87, 0.95, respectively for
Default vs. Default+Information, Default vs. Default+Purpose, and De-
6At that time, ”TheCompensators*” offered to retire licenses at a price of 5.53 Euro.
Note that this price can be different from the actual spot-price at the time we conducted
the experiment, since ”TheCompensators*” buy batches of licenses at a specific price and
then retire them based on the donations they receive, irrespective of price-changes that
appear in the meantime.
7We assume that measuring reactance items before treatments would have introduced
an ”additional nudge” with a potential influence on contributions. Kruskal-Wallis tests
and Steel-Dwass-Critchlow-Fligner multiple comparison tests do not show any significant
difference between treatments for all state and trait reactance items. This suggests there
is no significant effect of treatments. However, we cannot completely exclude a potential
common impact of all treatments on reactance.
11
fault+Info+Purpose vs. Default+Information vs. Default+Purpose. In or-
der to further substantiate Finding 2, we conducted additional sessions for
the Control group, Default, and Default+Information groups. The number
of additional observations based on an a priori power analysis. The simula-
tion suggested that pooling data from all sessions allowed to detect a true
difference of roughly 1.15 EUR (Cohen’s d= 0.37) in mean contributions
between the Default and Default+Information group 78.81 % of the time.
4. Results
We present and discuss findings in the following way: First, we demon-
strate main results regarding the effectiveness of defaults and their interrela-
tion with transparency. Second, we analyze the measures used to investigate
the relevance of psychological reactance to transparency of defaults.
4.1. Default effects
Overall, 498 subjects contributed 1,385.5 Euro to retire carbon licenses,
resulting in 2.78 Euro per subject. Of all participants, 68.27% contributed
a positive amount, and 9.44% opted for the default value. Table 2 presents
summary statistics of the variables divided by experimental groups. Figure 1
presents the respective mean contributions.
[Table 2 about here]
[Figure 1 about here]
A Mann-Whitney test of H1 rejects the null hypothesis of equal con-
tributions between Control vs. Default (W= 5486, p = 0.001), Control
vs. Default+Info (W= 4974, p < 0.001), Control vs. Default+Purpose
(W= 1275, p = 0.032), and Control vs. Default+Info+Purpose (W=
1376.5, p = 0.046). Overall, we find evidence for a default- and pull-effect.
To check robustness of the default effect we focus on contributions as
an outcome variable in Tobit regression. The Tobit model accounts for left-
censored contributions and allows testing effects on the latent, unobserved
contribution variable. This means we assume that at least some subjects
would choose to take from instead of contribute to the public good. Thus, we
interpret the dependent variable as desired contributions, and indeed even
damages, to climate protection. This assumption is common in dictator-
games and empirically valid (Engel, 2011).
12
We begin with a restricted model limited to the treatment variable,
then add a dummy variable indicating that subjects perceive climate pro-
tection to be (very) important, and proceed to add other relevant covari-
ates shown in Table 3. The reason we add importance to protect the cli-
mate separately is that a Chi2-Test rejects the hypothesis that subjects are
equally distributed among the treatment groups with respect to this variable
(χ2(4) = 34.37, p < 0.001).
[Table 3 about here]
By controlling for this variable we ensure that estimates of treatment
effects are not conditionally biased. Because the questionnaire is taken by
subjects after being exposed to treatments, there is a risk of the respective
manipulations being the reason for the differences in importance-ratings. Re-
garding Tobit models in Table 4, un-restricted model (3) includes all covari-
ates, i.e. rating of the importance of climate protection, gender, age, no
previous experience with experiments, judgment of buying emission licenses
from the EU ETS as an ineffective tool for climate protection, and a location
dummy.
Model (1) predicts that a mere default, a default plus info, and a de-
fault plus its purpose lead to higher average contributions compared to
no default. The effect of Default+Info+Purpose is marginally significant.
When controlling for subjects’ perception of the importance of climate pro-
tection in model (2), coefficients change. This results in significance for De-
fault+Info+Purpose. Importance of CP positively predicts the latent contri-
bution variable. A likelihood-ratio test suggests that model (2) fits the data
significantly better than model (1) (χ2(1) = 33.09, p < 0.001). Controlling
for additional covariates increases precision of the estimated average treat-
ment effects. A likelihood-ratio test suggests that un-restricted model (3) fits
the data significantly better than restricted model (2) (χ2(5) = 66.40, pp <
0.001).
F1: There is a default effect on contributions for a default, a default plus
information, a default with added purpose, as well as for a default with both
types of transparency.
[Table 4 about here]
13
4.2. Influence of transparency on default effectiveness
A Kruskal-Wallis test for equal contribution distributions in the treatment
groups is not significant (H(3) = 0.484, p = 0.922). So are respective pairwise
comparisons with Dunn’s test (not reported). Consequently, there is no
evidence for either of H2, H3, and H4.
As above, we augment our analysis by focusing on contributions in step-
wise Tobit-regression (Table 4). In un-restricted model (3), an omnibus
Wald-test for equality of parameter estimates for Default, Default+Info, De-
fault+Purpose, and Default+Info+Purpose does not lead us to reject the null
hypothesis (F(3,488) = 0.49, p = 0.692). The same holds for the restricted
models. There is no evidence of unequal contributions in the treatment
groups. Consequently, there is no evidence that transparency significantly
reduces contributions.8
F2: Informing participants that the default may have an influence on their
decision does not significantly decrease contributions compared to when they
are not informed.
F3: Informing participants about the default’s purpose does not signifi-
cantly increase contributions compared to when they are not informed.
F4: Informing participants that the default may have an influence on
their decision, as well as of the default’s purpose does not decrease or in-
crease contributions, compared to the other types of transparency (including
no transparency at all).
Of the additional covariates, Gender and EU ETS not effective are sig-
nificant. Being male, as well as judging the EU ETS as not effective to
protect the climate, negatively predict the latent outcome variable. The for-
mer finding is consistent with evidence from dictator games (Engel, 2011).
Findings on gender differences in public good games are ambiguous, however
(Croson & Gneezy, 2009). In the context of real contributions to climate
protection, evidence by Diederich & Goeschl (2014), while suggesting that
female subjects are less indifferent to climate protection, do not support a
8Estimated treatment-effects of un-restricted regression models are plotted in Appendix
B (Figures B.5, B.6, and B.7).
14
higher willingness to pay for emission certificates of women. Findings with
respect to age somewhat align with those of Borghans & Golsteyn (2015) who
find, in a less restricted sample, that the default effect does vary with age.
However, at around 22 years (the mean of our sample) they find a relatively
large default effect. This may explain why we find a default effect, but no
effect of age.
4.3. Psychological reactance and transparency
To test if reactions towards the combination of a default value with dif-
ferent types of transparency can be explained by psychological reactance, we
measured subjects’ proneness to experience psychological reactance.9
Specifically, we test whether subjects’ reactions towards different types
of transparency accompanying the default differ depending on subjects’ trait
reactance. Therefore, we run regressions with an interaction term of the
treatment variable and the trait reactance index. The latter is centered on
the mean, so that treatment-main-effects are meaningful (Table 4). Note that
this regression excludes observations from the control group. For reasons
of brevity, we focus on the main effects of trait reactance, as well as on
interaction-effects.
As in previous Tobit models, model (5) fits the data better than model
(4) (χ2(1) = 28.42, p < 0.001), and model (6) fits the data better than
model (5) (χ2(4) = 50.11, p < 0.001). We find no significant main effect of
trait reactance, nor do we find that the different types of transparency and
the trait reactance index interact significantly for any of the three model-
specifications. In other words, there is no evidence that the effect of different
types of transparency on average contributions is conditional on subjects’
trait reactance.
F5: The influence of information on the default effect does not depend
on the level of trait reactance of participants.
9To create an index for trait reactance, we constructed dummy variables for each of
the 14 items of the scale, which are equal to 1 when the subject responded with ”Agree”
or ”Strongly agree” to the respective question, 0 otherwise. We then added the dummies
for each subject to create the index, which ranges from zero to 14. Findings are consistent
for trait reactance included as a (un-weighted) factor-based score.
15
In order to test whether reactions to different types of transparency can
be explained by psychological reactance, we create an index for each of the
two state reactance-categories, i.e. for the perceived threat to freedom and
the anger-category.10
We model the log odds of subjects being in a higher level of each of both
ordinal indexes on all explanatory variables used above (Table 5). Note that
this regression excludes observations from the control group since subjects in
this group were not presented with the default option which they could rate.
None of the coefficients modeling treatment effects are significant.11
F6: Combining the default with information about its potential behav-
ioral influence does not increase participants’ experience of state reactance.
Age negatively predicts experienced anger triggered by the default value.
The finding that experiencing negative emotions decreases with age is known
in the literature (e.g. Charles et al., 2001).
[Table 4 about here]
Both approaches that are linking different types of transparency of a
default to psychological reactance suggest that subjects neither perceive a
default value differently based on the type of transparency accompanying it,
nor does their inherent propensity to show psychological reactance change
the way they react to these different types of transparency.
5. Discussion and conclusion
The experiment advances the discussion of nudges and transparency by
providing empirical evidence on the effect of transparency on the performance
of a pro-environmental default value. Despite the widespread application of
nudges, many researchers and consumers are concerned of the potentially
10We constructed a dummy-variable, which is equal to 1 when the subject ”agreed”
or ”strongly agreed”, resp. replied with ”to some extent” or ”very” to the respective
statements, for each item (see Appendix C). Then, we added the respective dummies in
each category, to form two indexes, each ranging from zero to four. Findings are consistent
for when both dependent variables are included as (un-weighted) factor-based scores in
linear OLS-regression.
11This finding is consistent with non-parametric tests for differences of individual items
of the scales (not reported).
16
manipulative nature of behavioral interventions. In democratic societies,
public authorities are expected to be transparent with regard to their actions
and intentions. Therefore, covertly ’exploiting’ people’s psychological biases
potentially inhibits perceived legitimacy, and ultimately effectiveness of such
policies. The most straightforward solution to this problem is to instruct
policy-makers to disclose information regarding the potential influence of the
nudge, and its purpose. However, this suggestion raises the concern that
nudges will no longer be effective. As expressed by Bovens (2009), nudges
”work best in the dark”. The results of this study suggest that this concern
might be overstated.
The experiment provides evidence that defaults increase contributions
to climate protection even when complemented by disclosure regarding the
potential influence of the default, its purpose, or both. Furthermore, there
is no evidence that information on the potential behavioral influence and/or
purpose of the default triggers psychological reactance. Likewise, there is no
evidence that subjects differing in their proneness to experience reactance
also differ in how they react towards the default with additional information.
These findings suggest that despite the initial concern over the inhibiting
influence of transparency, nudges in the form of defaults can be transparent
and at the same time effective. In order to preserve the effect of defaults
and increase the legitimacy of behaviorally informed policies, policy makers
should be transparent about their motives, as well as the potential behavioral
influence of the instrument. The motive and how it is perceived by the
decision maker has been found to matter for advice (Kuang et al., 2007).
Our findings replicate and add to previous evidence on the influence of
transparency. Loewenstein et al. (2015) and Kroese et al. (2016) reported
that pro-self defaults were effective in health contexts even after disclosing
information about them. Our study extends this conclusion to pro-social
nudges, a type that is widely used in the context of public policy-making.
Moreover, we extend findings of Steffel et al. (2016) by examining the influ-
ence of transparency in a more realistic setting where participants’ decisions
have an actual consequence for them, and for the environment. Findings are
also useful for the private sector and NGOs aiming to include nudges in their
inventory to increase contributions to environmental protection, and possibly
other public goods, e.g. charity.
Although several recent studies link nudges to psychological reactance,
they do so either indirectly, or they deal with hypothetical and attitudinal,
instead of behavioral outcomes (Haggag & Paci, 2014; Arad & Rubinstein,
17
2017; Loewenstein et al., 2015; Hedlin & Sunstein, 2016). By measuring both
state and trait reactance, we enable a more direct way of assessing the inter-
action of psychological reactance with the influence of transparency on the
effectiveness of a default value. To our best knowledge, Goswami & Urmin-
sky (2016) is the only study that assesses the interaction of trait reactance
with the size of a default value on behavioral outcomes, i.e. charitable giv-
ing. They find no significant interaction effect. On a more general level, our
findings, in line with theirs, suggest that psychological reactance plays a mi-
nor or no role with respect to behavioral effects of defaults, and, in our case,
transparency. In fact, a possible explanation of this might be the relatively
high default value, which is 80 % of the experimental endowment. Instead
of eliciting psychological reactance, such a high default might lead subjects
to ignore it altogether.
Findings suggest that the default value is an effective way of increasing
individual voluntary contributions to climate protection. Increased aggre-
gate contributions are consistent with inertia, as well as anchoring. A higher
fraction of participants picking the default value instead of specifying another
amount in the default, compared to the control group, supports the inertia/
effort reduction explanation. However, deviation costs in the experiment are
marginal (the subject had to make two mouse-clicks, as well as to type in
the contribution amount, instead of just making one mouse click on the de-
fault button), and contributing the default value is also consistent with an
anchoring explanation: Subjects may choose the default value not only be-
cause of inertia, but also because they consider this value first and only then
employ reasons against it, conditional on what they wanted to contribute
initially. This anchoring-explanation is consistent both with picking the de-
fault and moving towards the default, whereas inertia is only consistent with
the former behavior (Dhingra et al., 2012).
We observe that subjects who contribute a positive amount do contribute
more on average, when there is a default value with either type of trans-
parency, but the differences to the control group are not significant. Addi-
tionally, we observe an increase of subjects giving a positive amount due to
the default, which is consistent with the anchoring explanation. Together,
our findings suggest that increased aggregate contributions in the default
groups are due to an increase of the fraction of subjects contributing, as well
as of an increase of the fraction of subjects choosing the default value, but
not because of increased average contributions of subjects that contribute.
Inertia, as well as anchoring may therefore both be reasons for why we ob-
18
serve default effects. Intuitively, we would expect anchoring to play a more
pronounced role in real world applications of pro-environmental nudges, es-
pecially if defaults result in repeated and/or significant financial costs. For
someone who highly values environmental- and climate protection, deviat-
ing from a default, which may be perceived as conveying information about
social norms, can incur non-financial costs, especially if he or she aims to up-
hold a positive self-image. Maintaining a positive self image, as well as being
consistent with social norms, can be achieved by decreasing (not necessarily
closing) the gap between default value and initially intended contribution.
Note that our design does not allow to unambiguously identify the underly-
ing mechanisms causing the default effect in the experiment. Anchoring is
consistent with the interpretation of the default value as an implicit recom-
mendation, a persuasion attempt, coordination device, or a reference point.
If a decision maker regards the default as an implicit recommendation, she
may consequently increase/decrease her donation relative to her preferences,
after seeing the default. However, we cannot identify whether she interpreted
the default as a recommendation.
Furthermore, while being able to differentiate between the effects of dif-
ferent types of transparency is insightful for policy-makers, the difference
between the information and purpose treatments is not analytically clear.12
Communicating the purpose of the default implicitly reveals that the default
is expected to have an effect on individual decision making, without spelling
it out. Still, we think that the findings concerning this type of transparency
are important for practical purposes.
Further research could evaluate the role of trait reactance on how sub-
jects respond to different types of transparency for different types of nudges,
i.e. social norms or framing. Additionally, building on the shortcoming of
our experimental design, further studies should further investigate the link
between transparency and the different underlying working mechanisms of
defaults and other types of nudges. Since our experiment has a rather lim-
ited amount of subjects, field experiments can establish statistically more
powerful findings for interaction effects. Due to a more realistic context, a
field experimental approach would also increase external validity. Neverthe-
less, our experiment is less abstract than a ’regular’ laboratory experiment
due to the fact that contributions have a real effect on climate protection
12We thank an anonymous reviewer for this remark.
19
Harrison & List (2004). The current study focuses on one type of nudge,
and a specific context. Further research is needed in order to determine the
overall influence of transparency on the effectiveness of nudges. Moreover,
results might be context-specific, thus requiring further investigation into
pro-social nudges. Delving into the welfare implications of transparency can
also become a promising research endeavor (Sunstein, 2015).
Overall, our findings advance the understanding of how nudges in general,
and defaults specifically, affect individual behavior with social consequences,
and how policy-makers can increase their transparency without limiting their
effectiveness.
20
Acknowledgements
We thank Christoph Engel, Olexandr Nikolaychuk, Oliver Kirchkamp,
and other participants of the IMPRS Summer School 2015, Jena, for their
valuable comments. In addition, we would like to thank the participants
of the Behavioural Insights in Research and Policy Making SABE/IAREP
Conference, Wageningen; the 11th Annual Conference on Empirical Legal
Studies (CELS), Duke University; a guest lecture at the faculty of Gover-
nance and Global Affairs, Leiden University; Experiments at the Crossroads
of Law and Economics Workshop, Rotterdam, The Netherlands, for their
useful suggestions. Also, we thank participants of the 2nd Workshop on Ex-
periments for the Environment in Bremen, Germany; as well as Nieke Elbers
and participants of the Empirical Legal Studies Workshop at the University
of Amsterdam. Finally, we would like to thank Claudia Schwirplies, Jaroslaw
Kantorowicz, and Maximilian Kerk for their help. All possible mistakes re-
main, however, our own.
Funding
We are grateful for the financial support provided by the Innovation Pro-
gramme, Erasmus School of Law, Erasmus University Rotterdam, as well
as the Graduate School of the Faculty of Business, Economics and Social
Sciences at University of Hamburg.
21
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26
Table 1: Experimental design
Experimental group Default value Transparency information
Control No No information
Default 8 Euro No information
Default+Info 8 Euro
”Please consider that the preselected
default value might have an influence
on your decision.”
Default+Purpose 8 Euro
”Please consider that the preselected
default value is meant to encourage
higher contributions for the climate
protection fund.”
Default+Info+Purpose 8 Euro
”Please consider that the preselected
default value might have an influence
on your decision. This is meant to
encourage higher contributions for
the climate protection fund.”
Notes: The table reports the experimental group, the respective default value
presented to participants, as well as the respective transparency information as
it was shown to the subjects.
Table 2: Descriptive statistics of all outcome variables to assess the default effect
Contri- Con- Picked n
bution tributed default
Group Mean SD Mean Mean
Control 1.82 2.66 51.76 0 85
Default 2.95 2.98 70.76 12.28 171
Default+Info 3.04 2.98 74.07 8.02 162
Default+Purpose 2.92 3.19 71.79 15.38 39
Default+Info+Purpose 2.85 2.95 65.85 17.07 41
Notes: The table reports summary statistics (means and standard
deviations) of different outcome variables, as well as the number of
subjects per experimental group. Outcome variables are: contri-
butions to the climate protection fund, the percentage of subjects
contributing a positive amount, as well as the percentage of sub-
jects contributing the default value.
27
Figure 1: Mean contributions per experimental group
0
1
2
3
4
5
Control Default Default
+Info Default
+Purpose Default
+Info
+Purpose
Experimental group
Contribution [EUR]
Notes: The figure shows mean contribution levels in the experimental groups. Error bars
represent 95% confidence intervals.
Table 3: Descriptive statistics of covariates
Age
Gender Impor- No exp. EU ETS
(Male) tance Exp- not
of CP erience effective
Experimental group Mean SD Mean Mean Mean Mean
Control 23.75 4.94 48.24 76.47 23.53 60
Default 24.16 4.29 43.27 82.46 29.82 60.23
Default+Info 23.92 4.53 45.06 88.27 25.93 56.79
Default+Purpose 22.28 4.65 53.85 51.28 20.51 64.1
Default+Info+Purpose 22.68 3.72 58.54 63.41 19.51 58.54
Notes: The table reports summary statistics (means and standard deviations) of
different covariates per experimental group. Covariates are: age of participants,
percentage of males, percentage of subjects perceiving climate protection as (very)
important, percentage of subjects without prior experience with experiments, as
well as the percentage of subjects judging license retirement as an ineffective mean
for climate protection.
28
Table 4: Stepwise Tobit-models with and without interaction term
(1) (2) (3) (4) (5) (6)
Contribution Contribution Contribution Contribution Contribution Contribution
Default 1.868∗∗ 1.718∗∗ 1.659∗∗
(0.587) (0.571) (0.539)
Default+Info 2.056∗∗∗ 1.758∗∗ 1.670∗∗ 0.165 0.0152 0.00216
(0.586) (0.577) (0.538) (0.438) (0.429) (0.410)
Default+Purpose 1.8662.612∗∗ 2.528∗∗ -0.0343 0.858 0.841
(0.839) (0.845) (0.784) (0.730) (0.750) (0.775)
Default+Info+Purpose 1.628x1.9211.896-0.260 0.169 0.174
(0.829) (0.779) (0.779) (0.726) (0.670) (0.756)
Importance of CP 2.806∗∗∗ 2.350∗∗∗ 2.810∗∗∗ 2.353∗∗∗
(0.517) (0.502) (0.558) (0.534)
Gender (Male) -1.045∗∗ -1.065∗∗
(0.353) (0.391)
Age -0.0406 -0.0200
(0.0403) (0.0431)
No exp. Exp erience -0.577 -0.522
(0.425) (0.451)
EU ETS not effective -2.512∗∗∗ -2.329∗∗∗
(0.347) (0.368)
Hamburg -0.0494 -0.102
(0.453) (0.504)
React -0.0897 -0.0977 -0.0783
(0.106) (0.102) (0.0971)
Default+Info ×React -0.108 -0.109 -0.0764
(0.145) (0.141) (0.133)
Default+Purpose ×React 0.183 0.208 0.114
(0.276) (0.285) (0.250)
Default+Info+Purpose ×React 0.0646 0.0316 -0.0483
(0.224) (0.206) (0.190)
Constant 0.357 -1.824∗∗ 1.986x2.259∗∗∗ -0.0734 3.072∗∗
(0.497) (0.644) (1.094) (0.314) (0.563) (1.100)
Sigma 3.969∗∗∗ 3.848∗∗∗ 3.591∗∗∗ 3.888∗∗∗ 3.766∗∗∗ 3.550∗∗∗
(0.152) (0.153) (0.143) (0.153) (0.152) (0.147)
Observations 498 498 498 413 413 413
Log Pseudolikelihood -1088.416 -1071.872 -1038.671 -929.4 -915.187 -890.107
F (4, 494)=3.33 (5, 493)=8.64 (10, 488)=13.19 (7, 406)=0.76 (8, 405)=3.98 (13, 400)=7.36
Prob >F 0.010 <0.001 <0.001 0.624 <0.001 <0.001
Pseudo R20.007 0.022 0.052 0.002 0.018 0.044
Notes: The table reports estimates of Tobit models with contributions censored at 0 as the dependent variable, with and without interaction
terms. Robust standard errors are in brackets. Default+Info, Default+Purpose, and Default+Info+Purpose denote the respective treatment
group, with Default as the base category. React measures subjects’ proneness to experience reactance in a metric scale, and is mean centered.
Def+Inf ×React, Def+Pur ×React, and Def+Inf+Pur ×React are interaction terms of the transparency type with proneness to exp erience
reactance. Importance of CP is a dummy that takes the value 1 if the sub ject perceives climate protection as (very) important. Gender
takes the value 1 if the subject is male. Age denotes the age of the subject. No exp. Experience is a dummy which takes the value 1 if a
subject did not participate in another experiment before. EU ETS not effective is a dummy that takes the value 1 when a subject judges
license retirement as an ineffective mean for climate protection. Hamburg takes the value 1 if the subject is from the Hamburg, as opposed
to the Rotterdam sample. Significance levels: x(p < 0.10), (p < 0.05), ∗∗ (p < 0.01), ∗∗∗ (p < 0.001).
29
Table 5: Ordered logistic model of state reactance
(1) (2)
Threat To Freedom Anger
Default+Info -0.00294 -0.167
(0.199) (0.223)
Default+Purpose -0.0297 0.0868
(0.418) (0.453)
Default+Info+Purpose -0.0686 -0.560
(0.330) (0.470)
Importance of CP -0.0275 -0.334
(0.232) (0.276)
Male -0.0798 -0.300
(0.190) (0.217)
Age -0.0594∗∗ -0.0832∗∗
(0.0183) (0.0268)
Participated -0.0221 -0.0560
(0.192) (0.242)
EU ETS not effective 0.183 0.173
(0.191) (0.216)
Hamburg -0.0120 -0.325
(0.250) (0.260)
Cut 1 -3.125∗∗∗ -2.029∗∗
(0.528) (0.683)
Cut 2 -2.270∗∗∗ -1.126x
(0.524) (0.679)
Cut 3 -1.088-0.251
(0.517) (0.685)
Cut 4 0.346 0.508
(0.525) (0.718)
Observations 413 413
Log Pseudolikelihood -640.583 -443.190
Wald Chi2(9) 12.96 19.80
Prob >Chi20.165 0.019
Pseudo R20.008 0.024
Notes: The table reports estimates of ordered logit models with ratings of defaults
as threatening to freedom, and anger arousing as the respective dependent variable.
Robust standard errors are in brackets. Default+Info, Default+Purpose, and De-
fault+Info+Purpose denote the respective treatment group, with Default as the base
category. Importance of CP is a dummy that takes the value 1 if the subject perceives
climate protection as (very) important. Gender takes the value 1 if the subject is male.
Age denotes the age of the subject. No exp. Experience is a dummy which takes the
value 1 if a subject did not participate in another experiment before. EU ETS not effec-
tive is a dummy that takes the value 1 when a sub ject judges license retirement as an
ineffective mean for climate protection. Hamburg takes the value 1 if the subject is from
the Hamburg, as opposed to the Rotterdam sample. Significance levels: x(p < 0.10),
(p < 0.05), ∗∗ (p < 0.01), ∗∗∗ (p < 0.001).
30
Appendix A. Experimental design
Instructions
Welcome and thank you very much for participating in this experiment. This
experiment is about decision-making. Please read the following instructions
carefully. Everything that you need to know in order to participate in this
experiment is explained below. If you have any difficulties in understanding
these instructions please raise your hand and I will come to you. Please note
that communication between participants is strictly prohibited during the
experiment. Communication between participants will lead to the exclusion
from the experiment. The experimental procedure will be as follows. You
will receive 10 Euro. Please decide how much of the 10 Euro you would like
to spend on climate protection. You can choose freely how much, if any, you
contribute to climate protection (whole numbers between 0-10). Should you
decide to contribute, we will realize your contribution to climate protection
by buying and retiring carbon emission licenses from the European Union
Emissions Trading System (EU ETS) at the end of the experiment (please
read the respective paragraph below for a description). By this, you have
the possibility to make a real contribution to climate protection. The rest of
the money is your private pay-out that you will receive in cash at the end of
the experiment.
After making the decision you will be kindly asked to complete a short
questionnaire. Please note that your decisions in this experiment are anony-
mous and will not be revealed at any stage to the other participants. (If rele-
vant) a confirmation of the aggregated real payment to the climate protection
fund will be sent to all participants at the end of the whole experiment.
The Climate Protection Fund
If a person wants to protect the climate, emitting climate gases such as CO2
should be avoided. But it is possible to do even more: Individuals can buy
and delete emission certificates from the EU Emission Trading System (ETS)
through certified organizations and NGOs. By doing so, a private person re-
duces the amount of CO2which can be emitted by European industries, pro-
tects the environment and ensures that the development of climate-friendly
technologies is accelerated. In this experiment, the participants’ contribu-
tions to the climate protection fund will be used to buy real carbon dioxide
(CO2) emission licenses on the market of the European Union Emissions
Trading Scheme (EU ETS) via the website ”TheCompensators.org”. It is
31
one example of an NGO that allows ordinary people to directly participate
in the EU ETS scheme, and where they can make decisions on CO2reduc-
tions.
The following table shows how much kilograms of carbon you reduce with
your payment, and how much money you receive for yourself. The far right
row indicates the respective amount of reduced CO2relative to a Dutch
citizens’ average of 9163 kg of CO2emitted per year.
Payment to retire CO2-
allowances
Private
payout
CO2 abated
[kg]
Share of average emissions per
year per person
[%]
0
10 €
0
0%
1
9 €
181
2%
2
8 €
362
4%
3
7 €
542
6%
4
6 €
723
8%
5
5 €
904
10%
6
4 €
1,085
12%
7
3 €
1,266
14%
8
2 €
1,447
16%
9
1 €
1,627
18%
10
0 €
1,808
20%
For example, with a payment of 3 Euro to retire carbon licenses, you retire
542 kg CO2. This corresponds to approximately 6% of the average emissions
per capita per year of a Dutch person. As a private pay-out you get 7 Euro.
With a payment of 8 Euro to retire carbon licenses, you retire 1,447 kg CO2.
This corresponds to approximately 16% of the average emissions per capita
per year of a Dutch person. As a private pay-out you get 2 Euro.
32
Figure A.2: Experimental screen for Control
Notes: The figure shows the decision screen shown to participants in the Control group.
They could choose any integer between 0 and their endowment of 10 EUR. By clicking
on the red OK button, subjects went to the next screen, providing them with information
about the consequences of their decision, i.e. their payoff, their contribution, as well as kg
of CO2offset.
33
Figure A.3: Experimental screen for Default + transparency
Notes: The figure shows the decision screen shown to participants in the Default groups.
They could choose to contribute the default value of 8 EUR by clocking on the respective
red button, or they could click on the button below to choose any other amount. The
transparency message was written where indicated in the figure. The following screen
provided subjects with information about the consequences of their decision, i.e. their
payoff, their contribution, as well as kg of CO2offset.
34
Appendix B. Statistical analyses
Figure B.4: Distribution of contributions
0.00
0.05
0.10
0.15
0.20
0.25
0.30
0.35
0 1 2 3 4 5 6 7 8 9 10
Contribution [EUR]
Fraction
Notes: Shows the distribution of contribution amounts, more precisely the fraction of
subjects contributing the respective amount. The dashed line indicates the default value.
35
Table B.6: P-values for pairwise MW tests of Contribution
Control Default Default Default
+Info +Purpose
Default 0.001
Default+Info <0.001 0.665
Default+Purpose 0.032 0.843 0.591
Default+Info+Purpose 0.046 0.785 0.606 0.91
Notes: P-values of pairwise Mann-Whitney tests for equality of distri-
butions of contributions to the climate protection fund. Comparisons
are indicated by the treatment names provided in the first column and
first row, respectively. Significance levels: p <0.05 in bold, p <0.1
in cursive.
36
Figure B.5: Default and transparency effects on contributions for different base-categories
Control
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Rotterdam
Hamburg
Treatment effects:
-4 -3 -2 -1 0 1 2 3 4
Control
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Rotterdam
Hamburg
Treatment effects:
-4 -3 -2 -1 0 1 2 3 4
Control
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Rotterdam
Hamburg
Treatment effects:
-4 -3 -2 -1 0 1 2 3 4
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Reactance
Default
Default+Info
Default+Info+Purpose
Default+Purpose
Treatment effects:
Reactance effect:
Reactance interaction:
-4 -3 -2 -1 0 1 2 3 4
Notes: The figure graphically depicts results from some of the findings from the Tobit
models. Dots with horizontal lines indicate point estimates with 95% confidence intervals.
Dots on the zero line without confidence intervals denote the reference category. Models
(3) and (8) in Table 4 display the underlying regression results. The top left panel refers
to finding F1, the top right panel to F2 and F3, the bottom left panel to F4, and the panel
on the bottom right to F6. Covariates are not shown.
37
Figure B.6: Default and transparency effects on perceived Threat to freedom
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Treatment effects:
-.1 -.05 0 .05 .1
Notes: Dots with horizontal lines indicate point estimates with 95% confidence intervals
from marginal effects of ordered logistic models. Dots on the zero line without confidence
intervals denote the reference category. Model (4) in Table 5 displays the underlying
regression results (albeit not showing marginal effects). It refers to finding F5. Covariates
are not shown.
Figure B.7: Default and transparency effects on Anger
Default
Default+Info
Default+Purpose
Default+Info+Purpose
Treatment effects:
-.1 -.05 0 .05 .1
Notes: Dots with horizontal lines indicate point estimates with 95% confidence intervals
from marginal effects of ordered logistic models. Dots on the zero line without confidence
intervals denote the reference category. Model (5) in Table 5 displays the underlying
regression results (albeit not showing marginal effects). It refers to finding F5. Covariates
are not shown.
38
Appendix B.1. Comparing subjects from Rotterdam and Hamburg
We conducted experimental sessions in two different cities. Findings from
the first eleven experimental sessions relied on data solely from Rotterdam,
while additional observations where gathered in Hamburg primarily in order
to increase the reliability of the null result presented in F2 (and to a minor
degree F3-F4 by increasing the n in the control group). The number of addi-
tional observations gathered in Hamburg relied on an a priori power analysis.
Based on this analysis we conducted additional sessions to gather 284 addi-
tional observations for the Control, Default, and Default+Info groups. The
experimental protocol in all sessions was identical.
Table B.7 shows summary statistics of the main outcome variables dis-
aggregated by treatment and location of the experiment. Contribution dis-
tributions in the Control (W= 795.5, p = 0.329), Default (W= 3053.5, p =
0.528), and Default+Info (W= 2119.5, p = 0.092) groups do not differ by
location. The same is true for the remaining outcome variables. Figure
B.8 shows the mean contributions disaggregated by location and treatments,
including bars indicating 95 % confidence intervals. Mann-Whitney tests in-
dicate that, while the default effect is significant in the Rotterdam sample
(W= 707.5, p = 0.007), but not the Hamburg sample (W= 2040.5, p =
0.074), this is reversed with respect to the Default+Info effect, which is sig-
nificant in Hamburg (W= 1732.5, p = 0.009), but not in Rotterdam (W=
769.5, p = 0.084). Differences between Default and Default+Info are insignif-
icant in both samples (R: W= 1113, p = 0.302; H: W= 6799, p = 0.24)
Table B.8 shows summary statistics of the covariates included in the
regression models disaggregated by treatment and location of the exper-
iment. Aggregated over treatments, participants in Hamburg are on av-
erage older than participants in Rotterdam (M= 24.94(SD = 4.81) vs.
M= 22.16(SD = 3.45), t(494.84) = 7.517, p < 0.001), less likely to be
male (M= 39.08 vs. M= 57.01, χ2(1) = 15.038, p < 0.001), and also
have a different distribution of study areas (χ2(6) = 156.65, p < 0.001). Ad-
ditionally, participants in Hamburg are more likely than their Rotterdam
colleagues to rate climate protection as (very) important (χ2(1) = 37.06, p <
0.001). They do not differ with respect to prior experience in experiments
(chi2(1) = 0.16, p = 0.69) or their views regarding the effectiveness of the
EU ETS (χ2(1) = 0.002, p = 0.961).
Aggregated over location, subjects are not balanced among treatments
according to some variables. Subjects’ ratings of the importance of climate
protection correlate with the treatment (χ2(4) = 34.37, p < 0.001). So does
39
age (H(4) = 16.294, p = 0.003), and the distribution of study areas (χ2(6) =
156.65, p < 0.001).
Figure B.9 shows standardized effect sizes and 95 % confidence intervals
of the relevant pairwise comparisons for which we gathered additional data.
While the effect size of the default effect (Con vs. Def) included zero in
the Hamburg sample, it does not include zero in the Rotterdam- and the
aggregate sample. The default+info effect size (Con vs. Def+Inf) is different
from zero in the Hamburg and aggregated sample, but not in the Rotterdam
sample. Although the standardized effect sizes for the Def vs. Def+Inf
comparison is opposite between Hamburg and Rotterdam, neither those nor
the aggregated sample exclude an effect size of zero. Figure B.10 shows
the regression coefficients and 95 % confidence intervals from Tobit model
(3). These are qualitatively similar to the respective effect sizes, with the
exception that the standardized effect size for the Con vs. Def comparison
in Hamburg includes zero, whereas this is not the case for the respective
regression coefficient.
40
Table B.7: Descriptive statistics of all outcome variables by experimental group and loca-
tion
Contri- Con- Picked n
bution tributed default
Group Location Mean SD Mean Mean
Control R 1.67 2.68 46.67 0 45
Control H 2 2.66 57.5 0 40
Default R 3.24 3.21 73.91 19.57 46
Default H 2.84 2.9 69.6 9.6 125
Default+Info R 2.49 2.95 67.44 6.98 43
Default+Info H 3.24 2.98 76.47 8.4 119
Default+Purpose R 2.92 3.19 71.79 15.38 39
Default+Info+Purpose R 2.85 2.95 65.85 17.07 41
Notes: The table reports summary statistics (means and standard deviations)
of different outcome variables, as well as the number of subjects per experimen-
tal group. Outcome variables are: contributions to the climate protection fund,
the percentage of subjects contributing a positive amount, as well as the per-
centage of subjects contributing the default value. Statistics are disaggregated
by experimental group and location of the experiment.
41
Table B.8: Descriptive statistics of covariates by experimental group and location
Age
Gender Impor- No exp. EU ETS
(Male) tance Exp- not
of CP erience effective
Group Location Mean SD Mean Mean Mean Mean
Control R 21.8 3.08 60 57.78 31.11 57.78
Control H 25.95 5.7 35 97.5 15 62.5
Default R 22.02 2.79 60.87 78.26 30.43 60.87
Default H 24.95 4.48 36.8 84 29.6 60
Default+Info R 22.07 2.96 51.16 79.07 20.93 53.49
Default+Info H 24.59 4.81 42.86 91.6 27.73 57.98
Default+Purpose R 22.28 4.65 53.85 51.28 20.51 64.1
Default+Info+Purpose R 22.68 3.72 58.54 63.41 19.51 58.54
Notes: The table reports summary statistics (means and standard deviations) of different
covariates per experimental group. Covariates are: age of participants, percentage of males,
percentage of subjects perceiving climate protection as (very) important, percentage of sub-
jects without prior experience with experiments, as well as the percentage of subjects judging
license retirement as an ineffective mean for climate protection. Statistics are disaggregated
by experimental group and location of the experiment.
Figure B.8: Mean contributions by experimental group and location
0
1
2
3
4
5
Control Default Default+Info
Experimental group
Contribution [EUR]
Location
Rotterdam
Hamburg
Notes: Shows mean contributions by experimental group and location, including 95 %
confidence intervals.
42
Figure B.9: Effect sizes by location and for aggregated data
Con vs.
Def
Con vs.
Def+Inf
Def vs.
Def+Inf
-0.50 -0.25 0.00 0.25 0.50 0.75 1.00
Cohen’s d
Experimental group
Location
Aggregated
Hamburg
Rotterdam
Notes: Shows Cohen’s d for each pairwise comparison for which additional data in Ham-
burg was gathered, including the 95 % confidence intervals.
43
Figure B.10: Coefficients from tobit model by location and for aggregated data
Con vs.
Def
Con vs.
Def+Inf
Def vs.
Def+Inf
-3 -2 -1 0 1 2 3 4
Tobit regression coefficient
Experimenteal group
Location
Aggregated
Hamburg
Rotterdam
Notes: Shows estimated coefficients from Tobit model (3) for effect for which additional
data in Hamburg was gathered, including the 95 % confidence intervals.
44
Appendix C. Questionnaire
Questionnaire on covariates
What is you gender? O Male O Female
What is your age?
Have you participated in other experiments before today? O Yes O No
How important is climate protection for you? Please circle the most suit-
able answer.
O Not important at all O Not important O Indifferent O Important O Very
important
Do you think that buying real carbon dioxide (CO2) emissions licenses on
the market of the European Union Emissions Trading Scheme (EU ETS) is
an effective method to contribute to climate protection? O Yes O No
Questionnaire on state reactance
Please indicate to what extent do you agree with the following statements
on a 5-point response scale that ranges from the statement ”strongly dis-
agree” to the statement ”strongly agree”. (Perceived threat to freedom)
The default value threatened my freedom to choose.
The default value tried to make a decision for me.
The default value tried to manipulate me.
The default value tried to pressure me.
Please indicate to what extent do you agree with the following statements
on a 5-point response scale that ranges from the statement ”Not at all” to
the statement ”Very”. (anger)
45
Please indicate how irritated you were with regard to the given default
value.
Please indicate how angry you were with regard to the given default
value.
Please indicate how annoyed you were with regard to the given default
value.
Please indicate how aggravated you were with regard to the given de-
fault value.
Questionnaire on trait reactance
Please indicate to what extent do you agree with the following statements
on a p-point response scale that ranges from the statement ”strongly dis-
agree” to the statement ”strongly agree”.
Regulations trigger a sense of resistance in me.
I find contradicting others stimulating.
When something is prohibited, I usually think, ”that’s exactly what I
am going to do”.
The thought of being dependent on others aggravates me.
I consider advice from others to be an intrusion.
I become frustrated when I am unable to make free and independent
decisions.
It irritates me when someone points out things, which are obvious to
me.
I become angry when my freedom of choice is restricted.
Advice and recommendations usually induce me to do just the opposite.
I am content only when I am acting on my own free will.
46
I resist the attempts of others to influence me.
It makes me angry when another person is held up as a role model for
me to follow.
When someone forces me to do something, I feel like doing the opposite.
It disappoints me to see others submitting to standards and rules.
47
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Background: Nudges have been proposed as an effective tool to promote influenza vaccination of healthcare workers. To be successful, nudges must match the needs of the target healthcare workers population and be acceptable. Objective: To evaluate the effectiveness and the acceptability of an opt-out nudge promoting influenza vaccination among medical residents. Methods: The hypothesis were that an opt-out nudge would be effective, better accepted when applied to patients than to residents, and that prior exposure to a nudge and being vaccinated increase its acceptability and residents' sense of autonomy (the feeling of being in control of their choice about whether to get vaccinated). Residents were randomly divided into two parallel experimental arms: a nudge group and a control group. The nudge consisted in offering participants an appointment for a flu shot, while leaving them the choice to refuse or to reschedule it. Results: The analysis included 260 residents. Residents in nudge group were more likely to be vaccinated than residents in control group. There was a strong consensus among the residents that it is very acceptable to nudge their peers and patients. Acceptability for residents and patients did not differ. Acceptability was better among residents exposed to the nudge and residents who were vaccinated. Residents considered that the nudge does not reduce their control over whether to get a flu shot. The sense of autonomy was associated with nudge's acceptability. Conclusion: An opt-out nudge to promote influenza vaccination among medical residents can be effective and very well accepted. These data suggest that this approach can complement other vaccination promoting interventions and be eventually extended to other healthcare workers' categories and to general population, but should consider its ethical implications. More studies are needed to assess the nudge's effectiveness and acceptability on other populations.
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Careful attention to 'choice architecture' promises to open up new possibilities for environmental protection-possibilities that may be more effective than the standard tools of economic incentives, mandates, and bans. How, for example, do consumers choose between environmentally friendly products or services and alternatives that are potentially damaging to the environment but less expensive? The answer may well depend on the default rule. Indeed, green default rules may be a more effective tool for altering outcomes than large economic incentives. The underlying reasons include the powers of suggestion, inertia, and loss aversion. If well-chosen, green defaults are likely to have large effects in reducing the economic and environmental harms associated with various products and activities. Such defaults may or may not be more expensive to consumers. In deciding whether to establish green defaults, choice architects should consider consumer welfare and a wide range of other costs and benefits. Sometimes that assessment will argue strongly in favor of green defaults, particularly when both economic and environmental considerations point in their direction. But when choice architects lack relevant information, when interest group maneuvering is a potential problem, and when externalities are not likely to be significant, active choosing, perhaps accompanied by various influences (including provision of relevant information), will usually be preferable to a green default. © Springer International Publishing Switzerland 2016. All rights are reserved.
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Based on a series of pathbreaking lectures given at Yale University in 2012, this powerful, thought-provoking work by national best-selling author Cass R. Sunstein combines legal theory with behavioral economics to make a fresh argument about the legitimate scope of government, bearing on obesity, smoking, distracted driving, health care, food safety, and other highly volatile, high-profile public issues. Behavioral economists have established that people often make decisions that run counter to their best interests-producing what Sunstein describes as "behavioral market failures." Sometimes we disregard the long term; sometimes we are unrealistically optimistic; sometimes we do not see what is in front of us. With this evidence in mind, Sunstein argues for a new form of paternalism, one that protects people against serious errors but also recognizes the risk of government overreaching and usually preserves freedom of choice. Against those who reject paternalism of any kind, Sunstein shows that "choice architecture"-government-imposed structures that affect our choices-is inevitable, and hence that a form of paternalism cannot be avoided. He urges that there are profoundly moral reasons to ensure that choice architecture is helpful rather than harmful-and that it makes people's lives better and longer.