Environmental and Resource Economics

, Volume 64, Issue 2, pp 317–340 | Cite as

The Effects of Moral Licensing and Moral Cleansing in Contingent Valuation and Laboratory Experiments on the Demand to Reduce Externalities

  • Benjamin Ho
  • John Taber
  • Gregory Poe
  • Antonio Bento
Article

Abstract

Recent field experiments show that peer information can induce people to reduce their production of negative externalities. Related work in psychology demonstrates that inducing feelings of relative culpability in one domain can induce spillover pro-social behavior in another domain. We use a contingent valuation and parallel lab experiment to explore patterns of cross-domain responses to norm-based interventions. Asymmetric responses between those whose impacts are above or below the norm are found to be robust across decision settings. Substantial heterogeneity in responses is observed across a number of dimensions not explored in large field experiments, raising questions about the universality of peer-information effects and the design of such programs.

Keywords

Culpability Moral licensing Moral cleansing Guilt Peer information  Green electricity 

1 Introduction

Recent large-scale field experiments demonstrate that peer comparisons and social-norm nudges are effective tools for inducing the conservation of privately purchased goods that collectively create negative public externalities. Randomized residential electricity experiments that have monitored energy use and informed households of their personal consumption levels relative to a neighborhood norm provide evidence that energy consumers significantly reduce their energy consumption relative to a control group that does not receive such comparative information (Ayres et al. 2013; Allcott and Mullainathan 2010; Costa and Kahn 2010, 2013; Allcott 2011). Such behavioral change-based interventions, as opposed to more traditional price instruments, can indeed be powerful, especially amongst specific groups of the population. Ferraro and Price (2013), for example, study the effects of providing non-price interventions for household water use and find that, at least in the short run, the social-comparison effect is equivalent to that which would be expected if average prices were to increase by 12–15 %; in a study of residential electricity consumption, Ayres et al. (2013) estimate that non-price, peer comparison intervention induce the equivalent consumption response as a 17–29 % price increase.

While the average treatment effect has been shown to be significant, it is apparent that there is variation in response patterns to norm-based interventions. Notably, in a localized study of 290 households, Schultz et al. (2007) demonstrate that some households actually increase their energy consumption when they are informed that their baseline consumption is below the average of their peer group. In this same study, high-energy users significantly decreased their electricity consumption levels relative to the baseline, as expected from the focus theory of normative behavior (Cialdini et al. 1991). This asymmetry in treatment effects has been replicated, to an extent, in large scale field experiments with observations ranging from 75,000 to 600,000 households. However, rather than observing a strong perverse boomerang effect where peer information increases consumption, there more commonly seems to be a zero, or muted negative, effect on consumption patterns of low-use households. Allcott (2011) estimates that social-norm treatment effects are not significantly different from zero for the lowest three deciles of baseline electricity users, but that there is a significant mean treatment effect in high-use households ranging from about \(-\)3.7 % for the 8th decile to over \(-\)7 % in the 10th decile. Ayres et al. (2013) similarly find no significant treatment effect on two out of lowest three deciles of baseline electricity use (the second decile had a significant treatment effect of approximately \(+\)1 %), while consumption levels significantly decline by about \(-\)3 to \(-\)7 % for the top three baseline energy deciles. In a regression framework, Ferraro and Price (2013, p. 70) estimate that the “social norm effect for our high user group is approximately 94.1 % greater (5.28 vs. 2.72 % relative reduction) than for our low user group—a difference that is significant at the \(p<0.005\) level.” In all, while strong boomerang effects may not be evident, there does appear to be an important asymmetry in responses to social-norm interventions between households with above and below norm consumption levels.

Moreover, although responsiveness to norm-based messages have been demonstrated in a number of domains (e.g. Frey and Meier 2004; Cialdini et al. 2006; Salganik et al. 2006; Cai et al. 2009) recent research in the energy-social norms literature suggests that non-pecuniary effects may not be as universal as previously thought. Different socio-economic groups may have heterogeneous responsiveness to peer information. In interpreting these results, Costa and Kahn (2010) argue that:

behavioral economists have underestimated the role that ideological heterogeneity plays in determining the effectiveness of energy conservation “nudges”... we find that liberals and environmentalists are more responsive to these nudges than the average person. In contrast, for certain subsets of Republican Registered voters, we find that the specific “treatment nudge” that we evaluate has the unintended consequence of increasing electricity consumption. (p. 2)

In this paper we show that asymmetric and heterogeneous responsiveness of a spillover effect from peer information is manifested in both contingent valuation and laboratory economics experiments. Along the lines of Bateman et al. (2008), who demonstrated parallelism between contingent valuation responses, and “inconsistencies...found in everyday decisions involving real commitments” (p. 125), we argue that evidence of convergent behaviors across methods lends validity to each. Further, the survey application allows us to explore whether heterogeneity in response patterns occurs in demographic and other respondent-specific dimensions not able to be explored in large-scale field tests. The laboratory experiment permits exogenous control of the individual’s impact, avoiding possible endogeneity effects that may arise in field and contingent valuation studies.

The contingent valuation study calculates the household carbon footprint of a nationally representative sample of consumers by asking questions about their energy-related consumption habits. A carbon footprint is defined to be the number of tons of carbon dioxide emissions an individual is personally responsible for based upon his or her energy consumption decisions in a given year. We then induce feelings of relative culpability in the treatment group by providing them with information about how their household’s carbon footprint compares to others in the study and then elicit their demand for green electricity. In an effort to parallel the field contingent valuation study, the laboratory experiment has student subjects purchase “private commodities” (analogous to electricity) that generate a negative externality (analogous to pollution) for a group in which they are a member. A treatment group is given information about the private, pollution-generating choices of others and the subjects are subsequently given an opportunity to contribute to a fund that would reduce the negative harm created by the externality. In the taxonomy of Harrison and List (2004) we present results from a framed field experiment coupled with a conventional laboratory experiment. In our use of validating information treatments in online samples our approach is similar to recent work by Kuziemko et al. (2013) who take a similar approach in the domain of income inequality, though unlike their results, we find that the heterogeneity of the subject pool matters a lot in terms of treatment effect sizes.

Beyond demonstrating convergent validity between field experiments, economic laboratory exercises, and contingent valuation responses and identifying further dimension of response heterogeneity to social-norm nudges, our research contributes to the broader literature on norm-based conservation incentives. First, in contrast to energy and water conservation in which the psychological cues and economics savings are mutually reinforcing, our contingent valuation study of quantity demanded for “green electricity” and laboratory experiment study of contributions to a public good involve tradeoffs between private costs and societal or group gains. As such, our work extends the work of Shang and Croson (2009) and Chen et al. (2009) who show that some individuals are willing to bear additional monetary burdens in response to information about social norms. Second, much of the previous research on norm-based messaging has been confined to providing information about peer consumption in the domain of the desired conservation activity. For example, studies that seek to encourage towel re-use in hotels, provide information about towel re-use habits of others (Goldstein et al. 2008). At the same time some limited research suggests that social-norm information in one domain of decision-making affects decisions in other domains (Mazar and Zhong 2010; Keizer et al. 2008). These studies have considered moral licensing—learning you are more moral in one domain makes you less moral in another—and moral cleansing—learning you are less moral in one domain makes you more moral in another. Our research speaks to both and finds an asymmetric response. This asymmetry could produce a “moral rebound” effect—where acting pro-socially in one domain increases anti-social behavior in another domain—that limits the effectiveness of social-norm based policy interventions. Therefore, understanding such response patterns could significantly improve the design of interventions and explain the limited effectiveness of past trials. More mundanely, our design speaks directly to the effect of carbon footprint calculators on the demand for carbon offsets and green electricity.

Our main findings are that information about the behaviors of other people in one domain affects public provision behavior in contingent valuation and lab experiments in a different domain. In effect inducing cold prickles encourages the seeking of warm glows. This effect of social information is asymmetrical—the moral licensing effect for individuals better than the norm is larger than the moral cleansing effect for those whose consumption and negative externality effects are worse than the perceived norm. Finally, we demonstrate that systematic heterogeneity in responses to social norm nudges extends substantially beyond the political/environmental dimensions explored in Costa and Kahn’s field experiment. As we argue in the concluding section, these findings, in conjunction with emerging field research, raise questions about the universal efficacy of nudges vis-à-vis pricing incentives.

The remainder of this paper is organized as follows. In the following section we review previous economic and psychological conceptualizations of the notion of culpability or guilt in choice and valuation and how these concepts have been tested in laboratory and contingent valuation exercises. We then provide details on our experimental design and data. In the fourth section we provide empirical analyses of our experimental results with respect to asymmetry in response patterns above versus below norm respondents. The fifth section lends supporting evidence to the Costa and Kahn results, and expands the analysis of heterogeneity to demographic and respondent-specific characteristics available from survey data. Conclusions and discussion are provided in the final section.

2 Background and Experimental Design

2.1 Background on Culpability

In this research we explore how the desire to prevent a public bad is affected by an individual’s relative culpability, which we define to be the amount of social damage resulting from an individual’s actions relative to damages caused by others.1 Whereas the mechanisms that might induce conformity to a perceived social norm have been extensively studied in economics (see for example Bikhchandani et al. 1992; Ellison and Fudenberg 1993; Bernherim 1994; Akerlof and Kranton 2000; Glaeser and Scheinkman 2002), the mechanism of culpability has received less attention. Guilt has been explored in the psychology literature (see Baumeister et al. 1994 for a review). Perhaps most famously, Carlsmith and Gross (1969) induced guilt in subjects by having them administer electric shocks to another person, a confederate. Later, when subjects believe they have completed the experiment, they are asked to donate blood. Subjects who actually administered the shock are much more likely to agree to donate, relative to subjects who merely observed the shocking.

Building from psychological foundations and psychological game theory (see Geanakoplos et al. 1989), Charness, Dufwenberg and co-authors construct a general theory of guilt aversion in which decision-makers experience guilt if they believe they let others down (e.g. Dufwenberg and Lundholm 2001; Charness and Dufwenberg 2006, 2007; Battigalli and Dufwenberg 2007). With supportive results from “Trust Game” experiments, they propose that this general theoretical framework can be extended to specific instances, such as public goods games and social norms, where it seems plausible that decision-makers are affected by guilt. In doing so these authors take care to distinguish the role of guilt aversion from conformity: “A norm is a social moral expectation, a definition of which acts people in society will judge as right or wrong...Too many authors use “norm” just to mean “conformity in behavior”. (Dufwenberg and Lundholm 2001, p. 511).

Andreoni’s (1995) prior research on public goods suggests that such motivations may depend on whether the provision of the public good is framed positively or negatively. In Andreoni (1995), two groups of subjects participated in strategically identical public goods provision games, but with two separate framings. In one, the experiment was framed as providing a public good so that subjects would be motivated by warm glow altruism; in the other, the experiment was framed as avoiding a public bad, so that subjects would be motivated by a desire to avoid a “cold prickle” of guilt. Sonnemans et al. (1998) conduct a like set of experiments in a threshold provision setting, alternatively framing the experiments as provision to provide a public good and prevention of a public bad. In both the Andreoni and Sonnemanns et al. studies, the tendency to free ride was more prevalent in the negative framing. Similarly, Solnick and Hemenway (2005) present informal survey evidence where positional concerns matter more for public goods rather than for public bads.

A related asymmetry in pro-social behavior in experiments comes from how initial property rights are interpreted based on the framing of the question. Grossman and Eckel (2012) and List (2007) argue that the same strategic choice yield differing amounts of pro-social behavior when the action is framed as giving versus taking. Korenok et al. (2013) and Bardsley (2008) parameterize this interpretation and estimate models of social preferences given different environments.

In the specific area of environmental norms, Bamberg and Moser (2006) conduct a meta-analysis of the literature on psychological mechanisms that promote pro-environmental behavior, finding that both social norms and guilt are important correlates to pro-environmental attitudes and behavior. Clark et al. (2003) find that participation in a green electricity program is correlated with self-reported altruism and pro-environmental attitudes as measured by the New Environmental Paradigm (NEP). Brouwer et al. (2008) test the “passenger pays principle” to find that air travelers’ perceived responsibility for climate change, awareness of the environmental impact of flying, and the frequency of flying were all positively correlated with WTP for a per-flight carbon offset program. This notion of personal responsibility in creating public harm is an extension of what Kahneman et al. (1993) refers to as an “outrage effect”, in which people are willing to pay more to avoid an environmental problem if they think it is human-caused than if they think that it is an outcome of nature (Bulte et al. 2005). Kahneman et al. (1993) and Brown et al. (2002), amongst others have demonstrated this “outrage effect” on contingent valuation responses.

Our experiments complement the aforementioned literature by honing in on the individual culpability in contingent valuation and public goods experimental settings. We use peer information to manipulate the norm in a sequential setting most similar to the framing experiments of Andreoni (1995) and Sonnemans et al. (1998). Rather than split “Provision of Public Good” and “Prevention of Public Bad” samples as done in these studies, however, we employ a sequential framework: in the first stage of the experiment, we observe private decisions in a negative externality setting; the second stage involves a public goods contributions game in which contributions mitigate the negative effects of decisions in the first stage. We expect two main outcomes. For those who learn they contribute more to the negative externality than the perceived norm, i.e. have positive relative culpability, we expect they will be more altruistic in the second. For those who experience negative culpability, by learning they contribute less to the negative externality than the perceived norm in the first stage, we expect they will be less altruistic in the second. We find support for both of these effects, but that the former dominates. This “moral licensing” effect has been explored by Mazar and Zhong (2010) who find that those who are given the opportunity to purchase green goods are more likely to cheat on a subsequent exam. Similarly, in one field experimental test of the “broken windows” effect Keizer et al. (2008) show that observing others violate one social norm makes subjects more likely to violate other social norms. Our results further demonstrate that the effect predominates in those pre-disposed to provide more public goods in the second domain—for example Democrats, replicating in a lab and contingent valuation context the findings of Costa and Kahn (2010) who observed that the effect is limited to Democrats2 in a field experiment on electricity conservation. We extend their work to show that the heterogeneous effect likely exists along other dimensions as well.

2.2 Contingent Valuation Experiment

The broad objective of the contingent valuation survey was to gather information from participants that allowed us to calculate the household carbon footprint for each respondent and then elicit their quantity demanded for green electricity program given information about their own carbon footprint and, in some treatments, their carbon footprint relative to those of another survey participant. Participants for the online survey were recruited through The StudyResponse Project, a nationwide panel of 95,574 people. The diversity of the sample, as seen in the summary statistics in Table 1 will be important for our analysis. Participants were chosen at random and emailed the URL for the survey. For completing the survey, participants received $5. Invitations to participate were sent to 520 panelists (stratified to be nationally representative by age and race), and we received 297 completed surveys3 for an 81 % response rate.
Table 1

Summary statistics for contingent valuation experiment

 

By treatment group

Treated: by culpability

Control

Saw 11 tons

Saw 26 tons

High culpability

Low culpability

Green elec.

143.33

143.40

107.68

152.26

96.40

Demand (kWh)

(15.41)

(12.30)

(12.98)

(12.87)

(11.46)

\(\hbox {CO}_2\) Total

23.30

20.84

25.91

32.01

11.08

(2.35)

(1.85)

(2.64)

(2.34)

(0.67)

Relative culpability

 

9.84

\(-\)0.09

16.96

\(-\)9.38

 

(1.85)

(2.64)

(2.18)

(0.72)

NEP

34.01

35.25

34.65

34.37

35.82

(0.81)

(0.67)

(0.82)

(0.71)

(0.75)

Liberal

0.75

0.75

0.66

0.73

0.69

(0.05)

(0.04)

(0.05)

(0.04)

(0.05)

Children

0.58

0.50

0.53

0.63

0.36

(0.06)

(0.05)

(0.06)

(0.05)

(0.05)

Female

0.57

0.49

0.49

0.47

0.52

(0.06)

(0.05)

(0.06)

(0.05)

(0.05)

Age

37.61

37.50

40.39

36.86

41.20

(1.17)

(1.19)

(1.40)

(1.10)

(1.50)

Income

81.6

62.4

66.7

77.7

47.0

(4.03)

(5.75)

(5.65)

(4.83)

(3.08)

College

0.53

0.53

0.46

0.55

0.43

(0.06)

(0.05)

(0.06)

(0.05)

(0.05)

Democrat

0.41

0.46

0.34

0.41

0.40

(0.06)

(0.05)

(0.05)

(0.05)

(0.05)

N \(=\)

79

112

83

111

84

Standard errors in parentheses

\(\hbox {CO}_2\) total: total \(\hbox {CO}_2\) footprint

Culpability: total \(\hbox {CO}_2\) footprint minus 11 or 26 tons, depending on treatment

NEP: aggregate NEP value

Liberal: binary for liberal/conservative (1 if liberal)

Children: binary for children in household

Female: binary for gender (1 if female)

Age: age of respondent

Income: annual Household income in thousands USD

College: binary for education (1 if at least college education)

Democrat: binary for party affiliation (1 if democrat)

There were four steps in the survey: (I) Eliciting demographic questions to calculate the subject’s household carbon footprint; (II) Providing information about International Panel on Climate Change (IPCC) predictions on the impacts of climate change; (III) Showing subjects their estimated annual carbon footprint based on the input they provided; and (IV) Eliciting individual demand for green electricity. For the control treatment, subjects were not provided any information about the carbon footprint of others. All other subjects received information about the carbon footprint of “Others like you who took this survey” (see Fig. 1. Subjects completed each question in order and were not allowed to go back.
Fig. 1

Information about carbon footprint presented in the survey

Part I of the survey consisted of several web pages eliciting information about energy use, including housing characteristics (type, age, size of residence, and location), home energy use (monthly electric and gas bill expenditures, type of fuel used to heat house, whether the household generates or purchases electricity); automobiles (number, models, use of each vehicle) and transportation choices (use of public transportation, frequency of short and long domestic flights, frequency of international flights). Subjects were also asked about whether they purchased carbon offsets and if so, how many had they purchased. Only 31 subjects reported having purchased carbon offsets.

Subsequent to providing the above information, subjects were provided with three IPCC climate policy scenarios and their anticipated consequences as presented below in Table 2. The purpose of this screen was twofold. First, we wanted to make respondents aware of current climate projections and relative policy options ranging from “Business as Usual” to “Aggressive Emissions Reductions.” To a certain extent, this information also served to induce an element of moral outrage for those concerned about climate change.
Table 2

Information about climate change presented in on-line survey

Climate options the IPCC has presented several options for reducing climate change, each with different final levels of carbon and impacts on the global climate:

 

Business as usual

Small emissions reductions

Aggressive emissions reductions

Mean percent change in carbon emissions from 2000 to 2050

115 % increase

55 % increase

70 % decrease

Global average temperatures increases

8.8–11\(^{\circ }\) (4.9–6.1 \(^{\circ }\)C)

7.2–8.8 \(^{\circ }\)F (4–4.9 \(^{\circ }\)C)

3.6–4.3 \(^{\circ }\)F (2–2.4 \(^{\circ }\)C)

Sea level increases

12–24 inch (0.3–0.6 m) Millions at risk of coastal flooding

10–24 inch (0.26–0.6 m) Millions at risk of coastal flooding

\(<\)17 inch (0.45 m)

Extinction risk

More than 40 % of species face some risk

More than 40 % of species face some risk

30 % of species face some risk

Crops and famine

Crop productivity is expected to decrease. Global food production is expected to decrease, causing an increased risk of famine

Crop productivity is expected to decrease. Global food production is expected to decrease, causing an increased risk of famine

Crop productivity may increase in some regions and decrease in others. Increased risk of famine in some areas

Other effects

Increase in intensity and frequency of heat waves. Increased range for tropical diseases. Together, these will cause death and sickness, placing a substantial burden on health services

Increase in intensity and frequency of heat waves. Increased range for tropical diseases. Together, these will cause death and sickness, placing a substantial burden on health services

Increase in intensity and frequency of heat waves

In Part III, respondents were provided with an estimate of the carbon generated from their use of utilities and transportation and, after accounting for offset purchases, their estimated carbon footprint (“the total amount of climate changing greenhouse gas emissions caused directly and indirectly by your household”) in tons of carbon per year. Carbon footprints were calculated using two algorithms. If participants knew their electricity and heating expenditures, information about average electricity and fuel prices in each state were used to determine annual consumption of electricity and fuel (If participants knew their fuel expenditures but not their fuel source for heating, a weighted average of all fuel sources for the state was used.). Annual consumption of electricity was then converted into \(\hbox {CO}_2\) emissions using the average \(\hbox {CO}_2\) intensity for each state. Fuel consumption was converted into \(\hbox {CO}_2\) emissions using information about \(\hbox {CO}_2\) intensity for each fuel type. If participants did not know their electricity and heating expenditures, we gathered information about their housing structure and compared it to information about average energy consumption for houses of similar age, type and size in their state, which was then used to calculate \(\hbox {CO}_2\) emissions as above. Information about fuel prices, generation mix and average household energy consumption was obtained from the Energy Information Administration of the Department of Energy.

Information about participants’ cars and miles driven was directly computed based on combined city/highway fuel economy information from the EPA for every make, model and year of car from 1983 to 2009. For air travel, short flights were assumed to be 100 miles each way, long flights 750 miles, and international flights 4,250 miles. Carbon offsets reduced the carbon footprint by 168 pounds for every dollar spent, equivalent to prevailing rates at popular commercial carbon offset retailers.

Median estimated carbon emissions for the sample were 17.9 tons per household per year. For subjects in the control group, no other information was provided.4 Individuals in the treatment groups were informed that “Others like you who took this survey in the past had a carbon footprint of xx tons per year” and whether their contribution was MORE or LESS than this value. The “xx” value was randomly assigned to be high (26 tons) or low (11 tons). For example, as depicted in Fig. 1, a subject with an estimated carbon footprint of 18 tons and was assigned to the “See Low” group would be told that “Others like you who took this survey in the past had a carbon footprint of 11 tons per year” and that “Your contribution to global warming is MORE than this average.” Similarly, a like individual who was assigned to the “See High” treatment was “Others like you who took this survey in the past had a carbon footprint of 26 tons per year” and that “Your contribution to global warming is LESS than this average”. 26 tons and 11 tons were selected because they were the footprint from actual sub-samples collected during pilot experiments that happened to be near the 25th and 75th percentile of the total sample. This ensures that on average about half of all of those treated were informed that they were relatively more culpable than others, while half received information that they were relatively less culpable. As will be discussed below, the difference between the subject’s carbon footprint and the value associated with the reference individual provided a measure of relative culpability.

Given this information the demand for green electricity was elicited using a modification of a green electricity payment card used in Champ and Bishop (2001, 2006) in which individuals were given opportunities to buy blocks of energy measured in kilowatt hours. As shown in Fig. 2 each block had a corresponding monthly and annual cost and estimated annual tons of \(\hbox {CO}_2\) averted based on information available from the Energy Information Agency of the Department of Energy.
Fig. 2

Elicitation question for contingent valuation in on-line survey

In Part IV, debriefing and demographic questions were asked, along with ten questions designed to measure environmental concern drawn from the New Environmental Paradigm (NEP) scale (Dunlap and Van Liere 1978; Dunlap et al. 2000.) This scale is widely used in the psychology and sociology literature to characterize an individual’s environmental concern based on the extent to which they agree or disagree with various statements of environmental concern:

limits to growth, anthropocentrism, the fragility of the balance of nature, rejection of the idea that humans are exempt from the constraints of nature, and the possibility of an eco-crisis or ecological catastrophe. The modified NEP-scale is commonly used in the psychology literature and aims at capturing the following five facets of environmental concern: The response categories range between 1 and 5 so that high scores correspond to a stronger pro-environmental attitude than low scores (with the ordering reversed for the statements that reject the NEP-paradigm) (Ek and Soderholm 2008, p. 175)

Past studies of demand for green electricity have found the aggregated values across a series of NEP questions to be a significant, exogenous explanatory variable (Kotchen and Moore 2007; Ek and Soderholm 2008). We also asked subjects their political party identification, and political orientation on a Likert scale that ranged from “Very Liberal” to “Very Conservative”.

Twelve observations in our data set were identified as outliers and excluded from analysis: ten of these observations were excluded because at least one component of their carbon footprint was much greater than the rest of the sample, often an order of magnitude more. These observations were unrealistically high values, appearing to be incorrectly entered responses as to miles driven, airline flights, carbon offsets purchased, or housing information. The other two observations are repeated surveys. Removing these twelve observations halves the mean of the reported carbon footprint and reduces the standard deviation by an order of magnitude. Regressions with the outliers included returned the same qualitative results but were largely insignificant.

2.3 Lab Experiment

We conducted a parallel experimental economics laboratory in which subjects purchase “private commodities” (analogous to electricity) that generate a negative public externality (analogous to pollution) for a group in which they are a member. The subjects are subsequently given an opportunity to contribute to a fund that would reduce the negative harm created by the externality, akin, we believe to the opportunity to purchase green electricity.

Subjects (\(\hbox {n}=240\)) were recruited from a variety of undergraduate business and economics courses at Cornell University. Pen and paper experimental sessions were conducted in the Laboratory for Experimental Economics and Decision Research in cohorts ranging in size from 10 to 20. A session lasted approximately 45 min and average earnings were $14.41.

Subjects were randomly assigned into groups of five anonymous participants including themselves. Adapting elements of Plott’s (1983) seminal externality experiments,5 each individual was given a balance of $9 at the beginning of each of five rounds and a per-unit value (demand) function for a commodity that could be purchased at a cost of $1 (experimental dollars were converted to real dollars at a rate of $15 experimental \(=\) $1 real.). Subjects in each group were randomly assigned into high, low and medium demands (2 high, 1 medium, 2 small) and the choices offered to individuals were presented (see Appendix for full experimental instructions). Subjects were asked to read all of the instructions before beginning, but received no information about the choices of others except for the information from the experimental treatment.

In addition to private return for each commodity unit purchased, subjects were informed that each unit purchased would impose a negative externality on the entire group,

Your group also shares a GROUP FUND. This group fund began with 300 experimental dollars, and at the end of the experiment, any dollars in this group fund will be divided equally between all members of the group. Your actions and the actions of other people in your group in Round 1 may have reduced the total amount of dollars remaining in the group fund.

In Round [1–5], every unit of the commodity that you purchase decreases the number of experimental dollars in the group fund by 1.25. (Because there are five people in your group, every unit of the commodity that you purchase reduces the amount in the group fund by 0.25 dollars per person. Likewise, every unit of the commodity purchased by everyone else in the group reduces the amount in the group fund by 1.25 dollars and therefore costs everyone else 0.25 dollars.)

Hence, the optimal private decision would be to purchase only those commodities with a value of $1.25 or higher. Examples were worked through with the entire session on a whiteboard at the front of the lab, and after each decision, subjects were asked to calculate and report their own private returns and the impacts of their private decisions on other members of the group. Subjects were asked to sum their commodity purchases over the first five rounds and write this number down on a “passing sheet” which was submitted to the experimental moderator. The experimental moderator passed these sheets back to other subjects, who were then asked to record their own total purchases and the amount of total purchases that they saw on the sheet that was passed to them. Those in the high culpability treatment received the sheet of someone else with low demand, those in the medium culpability treatment received their own sheet, those in the low culpability treatment received the sheet of someone with high demand. Finally, subjects were each given the opportunity to play a public goods with the same group, where they could pay $1 to increase the group fund by $1.25. Amounts were chosen so that students could exactly offset their negative externality, although the words offset and externality were never used.

3 Analysis and Results

3.1 Contingent Valuation Experiment

Our analyses of the contingent valuation and laboratory experiments break the sample into treatment and control groups. In the contingent valuation “Treatment” group, subjects were informed about the carbon footprints of “Others like [them] who took this survey in the past”, with others like them corresponding to the “See Low” (\(\hbox {n}=111\)) and “See High” (\(\hbox {n}=84\)) information described previously. Similarly, the “Treatment” group in the Lab Experiment is organized by whether subjects were passed information from a subject with a “High” (\(\hbox {n}=63\)), “Medium” (\(\hbox {n}=29\)) or “Low” (\(\hbox {n}=62\)) induced demand. No such relative information was provided to the “Control” groups in the contingent valuation (\(\hbox {n}=79\)) and lab (\(\hbox {n}=64\)) experiments.

Averages for the control and treatment groups are provided in Tables 1 for the contingent valuation experiments. In the contingent valuation experiment, the dependent values reported are annual quantity demanded for green electricity. As these data are not conditioned on other possible covariates, some caution should be taken in interpreting the treatment effects. However, it is particularly notable that in both cases, providing information appears to either not affect average contributions or has a negative effect relative to the control group. The high culpability (11 ton) inducement yielded the same purchases of green electricity (214.0 kWh/year) as the control (213.8 kWh/year). The low culpability inducement led people to purchase less green electricity (160.7 kWh/year). This would suggest that providing social information tends to decrease purchases of the public good. The average level of green electricity purchased of the full treatment group was (191.3 kWh/year). If these results generalize, then contingent valuation studies that fail to provide information about peers would on average provide higher values than studies that provide such information, regardless of whether the individual is higher or lower than the norm. Such a result corresponds to the “broken windows” effect that observing others violate one social norm makes subjects more likely to violate other social norms (Keizer et al. 2008).

Columns (4) and (5) show the summary statistics divided by those who saw peer information lower (“high culpability”) or higher (“low culpability”) than themselves. While the green electricity demanded in these columns cannot be cleanly interpreted because membership in the low or high culpability treatment is endogenous and depends on the individual’s own carbon footprint, dividing the dataset in this way will be useful when we turn to regression analysis to understand the asymmetry in behavior. However, we address the endogeneity directly in the lab experiment.

Econometric modeling reveals more about the structure of how subjects responded to the peer information. In modeling the responses to the contingent valuation experiment, the dependent variable we use is “kWh per year of green electricity.” Given the discrete, ordered nature of the payment card response options, we adapt Cameron’s expenditure difference model (1988) for the interval modeling format developed in Cameron and Huppert (1989), wherein circling a particular threshold value provides the midpoint of an interval bounded from above by the midpoint between the selected value and the value above, and bounded below by the midpoint between the selected value and the value below. Assuming a logistically distributed contributions function, and letting \(\hbox {E(contributions)} = \upgamma \hbox {Z and var(contributions)} = \upsigma ^{2}\) yields the following log likelihood function:
$$\begin{aligned} Ln\left( L \right) = \sum \nolimits _{i=1}^n \ln \left[ {F\left( {{(\gamma Z_i -t_{iU} )}/\theta } \right) -F\left( {{(\gamma Z_i -t_{iL} )}/\theta } \right) } \right] , \end{aligned}$$
(1)
where F(\(\cdot \)) indicates the logistic distribution, Z is a vector of covariates, \(\hbox {t}_{\mathrm{iU}}\) is the upper bound of the interval selected, \(\hbox {t}_{\mathrm{iL}}\) is the lower bound, and the scale parameter \(\uptheta =\upsigma {\sqrt{3}}/\pi \). For the contingent valuation data used here, the bounds are the midpoint of the ranges below and above the selected value.
For the treatment group, we constructed a relative culpability variable measuring the difference between the subject’s carbon and the “other” carbon footprint he/she was shown.
$$\begin{aligned} \hbox {Culpability = Own carbon footprint -- Observed carbon footprint of others} \end{aligned}$$
(2)
In specifications where we include the control group which had no information about their peers, we set culpability to zero on the assumption that people assume their footprint is about the same as others. However, subjects in the control condition may have felt culpability just by being asked about their own demographic information. For this reason, the demographic controls may pick up some of the culpability effect for those in the Control condition. Hence we would expect including the controls in the regression to attenuate our estimates. Thus we focus on the regression specifications that drop subjects in the control condition. Columns (1) through (5) in Table 3 report regressions on Control and Treatment groups separately. In these regressions we also included controls for the subject’s own carbon footprint (\(\hbox {CO}_2\) Total), the NEP scale response summed over the 10 Likert scale NEP questions (NEP),6 and a self-reported political scale (Political Scale) variable extending from 0 (very liberal) to 6 (very conservative), which has been recoded into a binary variable for liberal political leaning at the median of the sample. These latter two variables comport with the environmental and political orientation variables in the Costa and Kahn study (2010). In addition, standard demographic and socio-economic variables of the type typically included in contingent valuation research (age, gender, children in household, income and education) are added as covariates.
Table 3

MLE results for contingent valuation experiment

 

(1)

(2)

(3)

(4)

(5)

Control

Treated

Continuous culpability

Conditional culpability

Full model

Short model

Full model

Short model

Relative culpability \(>\) 0

   

4.768***

4.470**

   

(1.785)

(1.797)

Relative culpability \(<\) 0

   

3.277*

2.956*

   

(1.769)

(1.773)

Relative culpability

 

4.012***

3.697***

  
 

(1.378)

(1.382)

  

\(\hbox {CO}_2\) total

0.935

\(-\)1.215

\(-\)0.868

\(-\)1.779

\(-\)1.414

(0.994)

(1.433)

(1.453)

(1.664)

(1.662)

NEP

8.693***

5.481***

6.113***

5.379***

5.989***

(2.775)

(1.485)

(1.400)

(1.485)

(1.407)

Liberal

3.383

10.09

 

9.878

 

(43.24)

(23.61)

 

(23.57)

 

Children

13.80

30.04

 

32.50

 

(40.04)

(21.98)

 

(22.28)

 

Gender

\(-\)36.72

\(-\)30.33

 

\(-\)29.53

 

(40.77)

(20.90)

 

(20.91)

 

Age

\(-\)0.159

1.502*

 

1.490*

 

(1.948)

(0.851)

 

(0.848)

 

Income

\(-\)7.433

\(-\)8.766

 

\(-\)8.412

 

(9.666)

(6.373)

 

(6.387)

 

Education

54.82

21.62

 

21.06

 

(39.79)

(21.58)

 

(21.58)

 

Constant

\(-\)110.7

\(-\)56.60

\(-\)47.99

\(-\)52.95

\(-\)41.83

(125.2)

(66.67)

(57.16)

(66.78)

(57.81)

Theta

87.89***

78.40***

80.41***

78.25***

80.25***

(8.963)

(4.993)

(5.099)

(4.988)

(5.094)

Observations

79

195

195

195

195

Log likelihood

\(-\)160

\(-\)398.1

\(-\)402.1

\(-\)397.9

\(-\)428.27

Standard errors in parentheses *** \(p<0.01\); ** \(p<0.05\); * \(p<0.1\)

Regressions in this table all include controls for politics, children, gender, age, income and education

Table 3 reports estimation results for Full Models with all the aforementioned covariates and Short Models with only a subset of the variables. The vector of covariates was organized into three sub-vectors: (1) Estimation Variables (Constant, Theta); (2) Culpability Measures (Relative Culpability \(>\) (\(<\)) 0; Relative Culpability, \(\hbox {CO}_2\) Total); and (3) Demographic Variables (NEP, Politics, Children, Age, Income, Education). For both the latter two groups the estimation strategy followed the pretest estimation procedure presented in Goldberger (1991) wherein Likelihood Ratio Tests were used to test the zero-null-vector hypothesis for the entire group (which was rejected in all cases). This was followed by a stepwise procedure in which the most insignificant coefficients were sequentially dropped. Coefficients were retained in the short model if their corresponding \(p\) values were less than the cutoff value of 0.15. Further, \(\hbox {CO}_2\) Total was kept as a control variable in all estimations.

Looking at the relative culpability variable in Table 3 reveals that though on average, those who received peer information were willing to contribute less than those who did not, people are indeed positively and significantly influenced by relative culpability—those who were induced to feel relatively more culpable were willing to pay more than those who were induced to feel relatively less culpable. Specifically, for each ton of \(\hbox {CO}_2\) a person is led to believe that she polluted more than others, her purchase of green power increases by around 4.01 kWh (the coefficient on Relative culpability in Column 2 of Table 3). For context, the average culpability as calculated by Eq. (2) for someone who saw a lower footprint was 16.96 tons, and the mean contribution for the control group was 213 kWh/year. In addition to the estimation variables, culpability, and \(\hbox {CO}_2\) Total, only the NEP covariate was retained in the Short Model.

To better reconcile the regression results with the aggregate effects, we interact binary variables for those with positive culpability scores (those who are induced to feel more culpable than others) and those with negative culpability scores (those who are induced to feel less culpable than others) with the relative culpability measure. This is referred to as “Conditional Culpability” in Table 3. Columns (4) and (5) present the results and find suggestive evidence that the impact of peer information is asymmetric. Those who are more culpable than those they observed significantly increase their contributions by 4.470–4.768 kWh for each ton of additional culpability. Looking at the relatively culpability for those who are less culpable (Relative culpability \(<\) 0), the effect is smaller and of lower insignifice, although the difference between the coefficients for positive culpability and negative culpability are insignificant (\(p\) value of 0.59 in an F-test). The lab experiment provides stronger evidence on this asymmetry.

Table 4 contains alternative specifications for the data. Column (10) presents the main specification with all outliers reintroduced, and consistent with the effects of measurement error, we get similar estimates but with magnitudes reduced. Columns (6) and (7) repeat our baseline specification but we combine the treatment and control. Combining the two adds the implicit assumption that those in the control condition feel some constant amount of culpability. If this assumption is violated, for example merely being asked to think about your carbon footprint induces feelings of culpability as well, then we would expect our coefficient on culpability to be attenuated as part of the effect of culpability would be picked up by footprint variable.7 In fact this is what we see.
Table 4

Additional specifications for MLE results for contingent valuation experiment

 

(6)

(7)

(8)

(9)

(10)

Control and treated combined

25th to 75th percentile households

Main spec w/outliers

Treated

\(-\)34.88*

\(-\)33.77

\(-\)50.12

\(-\)72.18*

 

(20.75)

(23.60)

(31.05)

(39.87)

 

Relative

 

2.271**

 

5.871

 

Culpability \(>\) 0

 

(0.979)

 

(4.968)

 

Relative

 

2.475

 

\(-\)0.831

 

Culpability \(<\) 0

 

(1.742)

 

(3.649)

 

Relative

2.324***

 

1.878

 

3.118**

Culpability

(0.817)

 

(1.971)

 

(1.447)

\(\hbox {CO}_2\) total

0.583

0.603

\(-\)7.766**

\(-\)8.591**

\(-\)3.084**

(0.741)

(0.768)

(3.365)

(3.463)

(1.445)

NEP

6.559***

6.567***

8.833***

8.968***

4.950***

(1.315)

(1.318)

(1.899)

(1.905)

(1.577)

Constant

\(-\)74.99

\(-\)75.51

\(-\)0.0804

4.276

7.849

(59.69)

(59.93)

(98.86)

(99.02)

(69.98)

Theta

81.76***

81.77***

75.03***

74.86***

84.73***

81.76***

(4.413)

(6.210)

(6.186)

(5.237)

Observations

274

274

117

117

204

Log likelihood

\(-\)560.9

\(-\)560.9

\(-\)236

\(-\)235.6

\(-\)429.3

Standard errors in parentheses *** \(p<0.01\); ** \(p<0.05\); * \(p<0.1\)

Regressions in this table all include controls for politics, children, gender, age, income and education

The culpability experiment introduces a further source of endogeneity in that a person’s culpability is also correlated with their household \(\hbox {CO}_2\) usage. Note that since we control for each individual’s \(\hbox {CO}_2\) total, the coefficient on culpability is identified off the exogenously assigned treatment group. There remains the concern that in this asymmetry, we are merely capturing the difference between those with high footprint and low footprint in a way that is not controlled for by the inclusion of the footprint variable (perhaps due to a non-linear relationship). This endogeneity concern can be addressed by using the subject’s assignment to either a high or low culpability treatment, as an instrumental variable, which is correlated with the perceived culpability of the subject, but uncorrelated with any subject characteristics.8 Another way to partially address this endogenity is to restrict our sample to only subjects between the 25th and 75th percentile of consumption.9 This way, for those who receive the treatment, whether they experience positive or negative culpability is entirely randomly determined by the treatment. Columns (8) and (9) present these results, but due to the loss of statistical power, coefficients on culpability are similar but insignificant. To fully address endogeneity concerns, we rely on the results from the lab experiment where footprint is exogenously assigned.

3.2 Lab Experiment

In order to better isolate the effect of culpability we rely on the results of a context-free lab experiment in which an individual’s culpability in producing a public bad is due to an exogenously induced demand for the private good. Since culpability depends only on own consumption levels and the observed consumption levels of others, the lab experiment allows a degree of exogenous control over both components.

Table 5 presents the summary statistics for the lab experiment. Note once again, that even though positive culpability was induced for two of the three treatment conditions, as before, all conditions yielded less (or at most equal) altruistic behavior than the control (3.36 tokens), although only one was statistically significantly. On average, it appears that information on culpability leads to less altruistic behavior in both CV and experimental laboratory settings.
Table 5

Summary statistics for laboratory experiment

 

Control

Entire sample

Treated

By induced demand

By culpability

Small

Medium

Large

High culpability

Low culpability

Round6

3.36

2.54

2.67

3.38

2.99

2.45

Purchases

(3.57)

(3.14)

(3.12)

(3.42)

(3.24)

(2.93)

Relative

(4.84)

4.46

10.76

(4.08)

15.05

Culpability

(8.37)

(7.97)

(10.36)

(12.21)

(8.45)

Total purchases

20.20

14.23

21.15

25.08

13.73

25.99

(9.92)

(4.68)

(6.01)

(10.96)

(5.56)

(7.72)

NEP

24.18

22.76

25.53

24.30

22.83

24.60

(5.49)

(5.08)

(6.02)

(5.74)

(4.98)

(6.25)

Liberal

0.59

0.69

0.54

0.53

0.61

0.58

(0.49)

(0.46)

(0.50)

(0.50)

(0.49)

(0.50)

Democrat

0.50

0.54

0.46

0.46

0.51

0.47

(0.50)

(0.50)

(0.50)

(0.50)

(0.50)

(0.50)

Obs

86

95

48

97

75

73

Standard errors in parentheses

Since each unit of a subject’s consumption choice generates negative externalities on others in the experimental session, we use their consumption choice as the analogue for “carbon footprint.” Also, in order to ensure the exogeneity of the culpability variable, we use the expected target footprint he would have been induced to select if he were a completely self-interested rationally maximized individual given the treatment condition he was in (high demand, medium demand, low demand) instead of using the subject’s actual own “footprint” minus footprint of others.
$$\begin{aligned} \hbox {Induced Culpability} = \hbox {Induced target footprint} - \hbox {Observed footprint of others} \end{aligned}$$
This measure of induced culpability is highly correlated (\(\rho = 0.7799\)) with actual culpability which was defined as actual footprint minus observed footprint of others, but ensures that the culpability score is exogenous and not correlated with subject characteristics like altruism, as is possibly the case in the CV experiment.
Table 6 presents the maximum likelihood estimates using a similar econometric model and estimation strategy as the one used for the CV experiment:one minor diffence is that here the quantity interval is bounded by the quantity selected and the next possible value. Similar asymmetric patterns emerge. In the continuous culpability model the coefficient on relative culpability is not significant in the full sample, nor are any other covariates When the estimation separates those who were either above or below the norms shown, those with relatively high induced relative culpability provide significantly more to the public good in the short, but not the full model. There is an insignificant effect for those with less relative culpability in both the full and short models for the treated sample. Note that we used a maximum likelihood model here to be consistent with the CV specification, but OLS and IV regressions using experimental assignment to instrument for culpability yielded similar results. OLS and IV specifications were clustered by experimental group.
Table 6

MLE results for laboratory experiment

 

Control

Treated

Full sample

Treated (outliers excluded)

Continuous culpability

Conditional culpability

    

Full model

Short model

Full model

Short model

Continuous culpability

Conditional culpability

Continuous culpability

Conditional culpability

Treated

     

\(-\)0.598

\(-\)1.440**

  
      

(0.458)

(0.597)

  

Relative

   

0.0505*

0.0502

 

0.0577*

 

0.06*

Culpability \(>\) 0

   

(0.0301)

(0.0306)

 

(0.0320)

 

(0.04)

Relative

   

\(-\)0.0496

\(-\)0.0478

 

\(-\)0.0880*

 

\(-\)0.03

Culpability \(<\) 0

   

(0.0441)

(0.0441)

 

(0.0470)

 

(0.05)

Relative

 

0.0134

0.0136

  

0.00342

 

0.02

 

Culpability

 

(0.0202)

(0.0203)

  

(0.0203)

 

(0.02)

 

Total

\(-\)0.0157

\(-\)0.0243

\(-\)0.0290

\(-\)0.0259

0.392

\(-\)0.0152

\(-\)0.0169

\(-\)0.01

\(-\)0.01

Purchases

(0.0442)

(0.0330)

(0.0328)

(0.0327)

(0.485)

(0.0273)

(0.0269)

(0.04)

(0.04)

NEP

0.0706

\(-\)0.0184

 

\(-\)0.0107

 

0.0141

0.0194

\(-\)0.05

\(-\)0.04

(0.0797)

(0.0410)

 

(0.0405)

 

(0.0382)

(0.0374)

(0.05)

(0.05)

Democrat

0.801

0.482

0.475

0.427

 

0.512

0.472

0.87

0.74

(0.852)

(0.491)

(0.484)

(0.490)

 

(0.444)

(0.440)

(0.56)

(0.56)

Session dum

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Constant

2.152

2.822*

2.452**

2.190

2.044*

2.832*

 

2.88*

2.42

(2.741)

(1.534)

(1.124)

(1.555)

(1.135)

(1.456)

 

(1.61)

(1.63)

Theta

1.866***

1.554***

1.589***

1.543***

1.578***

1.773***

1.755***

1.55***

1.54***

(0.173)

(0.108)

(0.109)

(0.107)

(0.108)

(0.0976)

(0.0965)

(0.12)

(0.12)

Obs.

82

150

154

150

154

232

232

119

119

Log likelihood

\(-\)214.1

\(-\)366.7

\(-\)379.4

\(-\)365.4

\(-\)378.2

\(-\)594.6

\(-\)592.3

\(-\)290.11

\(-\)289.27

Standard errors in parentheses

*** \(p<0.01\); ** \(p<0.05\); * \(p<0.1\)

Here again we see the asymmetric effect when one sees higher others compared to seeing lower others in the short model (F-test of the difference in coefficients, \(p=0.03\)). The negative, coefficients on culpability when culpability was less than zero is a bit puzzling. These effects however are largely insignificant, and appear to be driven by a few outliers who behaved in ways hard to reconcile with most typical theories (e.g. consuming at a point that was welfare destroying for both themselves and their group as a whole).

Therefore, in our final two columns of Table 6 we report our preferred specification, where we focus on the treated to account for the attenuation effect, and drop 14 of 240 observations corresponding to subjects that chose to consume more than what was even privately optimal in the first part of the experiment (i.e. they consumed at levels where the private cost exceeded the private benefit). As demonstrated, these results were qualitatively the same as those with outliers included.

4 Heterogeneity in Responsiveness to Norms

Costa and Kahn (2010) noted the heterogeneous effect of the peer information experiment on Democrats versus Republicans. We confirm their findings in Table 7 by dividing the data into self-identified “Democrats” (a relatively liberal party in the United States) and all others (Non-DEM). We extend their work by also considering heterogeneity in other dimensions, including number of children, gender, age, income, education, and NEP score, available for the relatively diverse contingent valuation study. Tables 8 and 9 decompose the effect of culpability by each of these demographic variables. Summary statistics and correlation tables are found in the appendix—note that although these demographic characteristics are correlated, the correlations are quite low, ranging from \(-\)0.11 (for attributes \(\hbox {CO}_2\) Total and Gender) to 0.19 (for attributes Age and NEP)
Table 7

MLE results for democrat/non-democrat split: contingent valuation experiment

 

Democrat

Not democrat

Full model

Short model

Full model

Short model

Relative

7.025**

5.714**

2.615*

2.263

Culpability

(2.745)

(2.430)

(1.576)

(1.655)

\(\hbox {CO}_2\) total

\(-\)4.110

\(-\)2.944

0.265

0.627

(2.600)

(2.482)

(1.678)

(1.759)

NEP

3.937

4.313

5.852***

6.650***

(2.834)

(2.762)

(1.649)

(1.609)

Liberal

\(-\)75.72

 

16.15

 

(65.43)

 

(25.65)

 

Children

37.82

 

29.40

 

(36.33)

 

(27.22)

 

Gender

26.93

 

\(-\)52.25**

 

(37.27)

 

(25.96)

 

Age

1.767

 

1.214

 

(1.670)

 

(0.954)

 

Income

6.996

 

\(-\)16.94**

 

(12.28)

 

(6.790)

 

College

11.43

 

32.50

 

(36.69)

 

(26.52)

 

Constant

17.13

60.90

\(-\)56.27

\(-\)99.61

(137.0)

(111.7)

(75.35)

(64.42)

Theta

82.49***

86.83***

70.31***

74.68***

(8.173)

(8.492)

(5.884)

(6.214)

Obs

80

80

115

115

Log likelihood

\(-\)162.2

\(-\)165.2

\(-\)228.6

\(-\)235

Standard errors in parentheses

*** \(p<0.01\); ** \(p<0.05\); * \(p<0.1\)

Table 8

MLE results for demographic subgroups for contingent valuation experiment (full regression)

Subgroup

Culpability coefficient

Liberal

4.045**

Not liberal

3.767*

Children

5.546***

No children

2.625

Male

4.131**

Female

3.545*

Age \(>\) 36.5

6.005***

Age \(<\) 36.5

1.548

Income \(>\) 4.7

7.220***

Income \(<\) 4.7

0.669

At least college

5.332***

Less than college

2.436

NEP \(>\) 34.5

5.34**

NEP \(<\) 34.5

2.377

Democrat

7.025**

Not democrat

2.615*

Each row reports the coefficient on culpability for the full regression run on the sub-group of the population specified

*** \(p<0.01\); ** \(p<0.05\); *\(p<0.1\)

Table 9

MLE results for demographic subgroups for contingent valuation

 

Long model

Short model

Relative culpability

4.564**

5.176***

(2.185)

(1.863)

Liberal (binary)

33.46

34.84

(23.96)

(24.22)

Culpability \(\times \) liberal

2.180

2.242

(1.448)

(1.366)

Children (binary)

28.18

19.79

(23.84)

(23.31)

Culpability \(\times \) children

(23.84)

(23.31)

(1.327)

(1.195)

Female (binary)

\(-\)17.61

 

(21.58)

 

Culpability \(\times \) female

\(-\)0.204

 

(1.290)

 

Age (binary)

1.873**

1.867**

(0.885)

(0.881)

Culpability \(\times \) age

1.050

0.521

(1.515)

(1.367)

Income (binary)

\(-\)8.674

\(-\)8.179

(6.892)

(6.698)

Culpability \(\times \) income

\(-\)0.656*

\(-\)0.532*

(0.379)

(0.310)

College (binary)

16.54

 

(22.52)

 

Culpability \(\times \) college

0.689

 

(1.483)

 

NEP (binary)

50.79**

47.57**

(22.85)

(22.68)

Culpability \(\times \) NEP

\(-\)1.530

\(-\)1.654

(1.187)

(1.027)

\(\hbox {CO}_2\) (binary)

\(-\)19.07

 

(32.15)

 

Culpability \(\times \) \(\hbox {CO}_2\)

1.223

 

(2.340)

 

Constant

82.19

77.15

(58.16)

(55.93)

Theta

78.84***

79.85***

(4.993)

(5.037)

Observations

196

196

Log likelihood

\(-\)401.8

\(-\)403.5

All variables are binary, continuous variables (like age and income) were made binary by splitting at the median. Standard errors in parentheses

*** \(p<0.01\); ** \(p<0.05\); * \(p<0.1\)

We first note that our results are consistent with Costa and Kahn (2010). As shown in the first two columns of Table 7, the coefficient on relative culpability for Democrats was positive and significant, indicating that such individuals are responsive to social norm nudges. Indeed, in the regression this parameter dominates in the sense that the coefficients for the other explanatory variables are not significant. As shown in the last two columns, however, neither the coefficient for Culpability nor for the \(\hbox {CO}_2\) Total is significant: non-democrats are not affected by our culpability inducement. Yet, coefficients for NEP and Political Scale are significant and consistent with expectations in the Non-Democratic regressions.

It is evident that this heterogeneity in response patterns extends to other dimensions. Table 8 parallels the approach used in Table 7. That is, we divide the sample into subsamples above and below the median, testing the null hypothesis that the coefficient on relative culpability is equal to zero. Such a test is of particular interest to those who are providing the nudge. Our results show that induced culpability is effective for liberals but not non-liberals; for those with children but not for those without children; for men but not for women; for those older than 36.5 but not those younger; for those above approximately $50,000 for income but not for those below; for those with a college degree but not for those without; for those who are more environmentally conscious (NEP score \(>\) 34.5). For brevity we only report the culpability coefficients for each estimation.

Table 8 decomposes the effect of culpability across different groups by considering a regression where culpability is interacted with all of our demographic variables, in effect testing the null hypothesis that the subsamples described above respond the same to nudges. This is done by creating constant and slope shift parameters for each demographic characteristic (the short model was created by eliminating all interaction terms that had a \(p\) value less than 0.15 in a Likelihood-Ratio Test). We find that when accounting for the entirety of measured demographic variables that people that are liberal, with children, have a relatively high income and high NEP scores behave significantly different than their counterparts.

A possible practical explanation for the patterns in Tables 7, 8 and 9 is that peer information nudges work on those already inclined to give, such as democrats, liberals and those with high NEP scores, but do not work and may even backfire when preaching to those less inclined (see Meier 2007a, b for a brief summary of related work on the importance of heterogeneity). It is also possible that in the specific context of climate change, those who question the premise of whether climate change is happening may be unresponsive.

We should be careful to note that this heterogeneity analysis should be seen as exploratory and mostly provided to be suggestive for future work. However, the fact that such heterogeneity exists appears quite robust. Awareness of this heterogeneity is important for increasing the precision of estimates of the effect of peer information interventions, as well as for increasing the cost effectiveness of future norm based interventions.

5 Conclusions

Using a contingent valuation framed field experiment coupled with a conventional lab experiment, we examine how peer information that induces culpability differs from the peer information interventions based on conformity that have been the traditional focus of the “nudge” literature. We demonstrate that there is important heterogeneity in how quantities purchased respond to culpability based peer information, and find similar patterns of heterogeneity for both the online contingent valuation experiment and the context free lab experiment using a convenience sample. We find that the culpability effect is larger when the information makes subjects feel good about themselves relative to when the information makes them feel guilty. We also find evidence that the effect of culpability comes mostly from those who may be more inclined to act more pro-socially.

These results have potentially important implications for public policy. It provides evidence on the usefulness of culpability as a separate channel than the norm and conformity based behavioral nudges commonly put forward. It also provides guidance to policy makers on how best to target such interventions on the sub-groups most likely to respond. However, our results also suggest caution on over reliance on informational nudges. Strategies that induce culpability primarily affect individuals who were already more inclined to reduce energy consumption in the first place. As a consequence, behavioral policies are less effective on the worst offenders and therefore can complement but cannot replace traditional policies like taxes or regulations that affect the entire population.

Footnotes

  1. 1.

    Our focus is on relative culpability because pilot experiments found that information about one’s absolute level of social damage without comparison to one’s peers had no effect on behavior.

  2. 2.

    The Democratic party in the Unites States is socially liberal or “left leaning”, while the Republican party is socially conservative or “right leaning”.

  3. 3.

    An additional 105 surveys were collected concurrently for an alternative treatment that is not reported here.

  4. 4.

    In pilot experiments, we also compared the results of a control group where no information about carbon footprint was given to the current control group where the carbon footprint was given without peer comparison and found no significant difference in behavior.

  5. 5.

    For the sake of simplicity, we did not include the double auction, and focused only on the demand side of the experiment.

  6. 6.

    The Cronbach alpha value for the subjects for the NEP questions was 0.7785, generally consistent with the literature, and indicating that the NEP is a coherent metric.

  7. 7.

    For example, consider a simple OLS regression where \(\beta _c\) is the coefficient on culpability, and \(\beta _f \) is the coefficient on footprint, and we estimate \(Y=\beta _C T+\beta _f f+\varepsilon \), where T is an indicator for the treatment group and f is the carbon footprint. If we assume those in the control group experience no culpability, we are then estimating in the model \(Y=\beta _f f+\varepsilon \) for those in the control so that the \(\beta _f \) variable will pick up part of the culpability effect.

  8. 8.

    These results are available from the lead author.

  9. 9.

    This approach was suggested by an anonymous external reviewer.

Notes

Acknowledgments

The author would like to thank William Schulze, as well as seminar participants at Cornell University, Peking University, Sydney University, Vassar College and the Economic Science Association for helpful comments.

Supplementary material

10640_2014_9872_MOESM1_ESM.docx (1.4 mb)
Supplementary material 1 (docx 1422 KB)

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Copyright information

© Springer Science+Business Media Dordrecht 2015

Authors and Affiliations

  • Benjamin Ho
    • 1
  • John Taber
    • 2
  • Gregory Poe
    • 3
  • Antonio Bento
    • 3
  1. 1.Economics DepartmentVassar CollegePoughkeepsieUSA
  2. 2.FERCWashingtonUSA
  3. 3.Cornell UniversityIthacaUSA

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