Holz, List, Zentner, Cardoza, and Zentner (2020) on Nudging Tax Compliance

Justin E. Holz, John A. List, Alejandro Zentner, Marvin Cardoza, and Joaquin Zentner, “The $100 Million Nudge: Increasing Tax Compliance of Businesses and the Self-Employed Using a Natural Field Experiment.” NBER Working Paper 27666, August 2020 (pdf here). 

• The tax authorities send you a message… 

• ...maybe the message just happens to mention the upcoming tax filing deadline: the control arm 

• ...maybe the message also notes the potential for your tax evasion to be publicized – one treatment arm, designed to increase the salience of social penalties for being a tax cheat. 

• ...maybe, instead of highlighting the public nature of identified tax evasion, the message notes the potential for your tax evasion to result in imprisonment – another treatment arm, designed to increase the salience of criminal penalties attached to tax evasion. 

• And for each of the three arms noted above, we can take half of the letter recipients and also mention in the letter that the tax authorities are prepared to potentially view mistakes in tax declarations, even honest mistakes, as intentional. (The notion is to frame evasion as a sin of commission, not of omission.) Mistakes imply that you were trying to be a tax cheat! 

• This very natural field experiment is conducted in the Dominican Republic, circa 2019, n≈56,000 firms and n≈28,000 self-employed people; tax evasion reportedly is rife in the Dominican Republic. 

• The field experiment applies to business entities subject to the corporate income tax and to self-employed taxpayers subject to the individual income tax. 

• The various messages are sent shortly before the tax filing deadline. 

• The threat of public disclosure of tax evasion dissuades tax evasion for both firms and individuals. 

• The “prison” message also reduces evasion, and for firms, about twice as effectively as the “publicity” message. 

• Framing evasion as an active choice, a sin of commission, in itself (without publicity or punishment prompts), does nothing (or worse than nothing), and likewise is ineffective if it is paired with the publicity notice. 

• But the combination of “intentional” framing with the prison message doubles the impact of the prison message. 

• The effectiveness of the interventions seems to arise from a decrease (by 20%) in potential taxpayers who declare (falsely, presumably) that their income is below the minimum required for taxation. 

• Large firms drive the reduced tax evasion – there is little or no compliance gain from the smallest 60% of taxpayers.

Shrader, Wooten, White, et al. (2017) on Using Loss Aversion to Motivate Students

Rebekah Shrader, Jadrian James Wooten, Dustin R. White, et al., “Improving Student Performance through Loss Aversion.” December 12, 2017; updated version available here.

• Pairs of nearly identical courses are offered, where one element of each pair calculates student points as losses from a perfect base: a score of 50 means the student has lost 50 points, as opposed to the usual (control) case where points accumulate with correct assignments. 

• The idea is to see if the “loss framing” triggers greater student effort in a bid to avoid or minimize losses (as opposed to hoping to acquire gains); that is, the authors are testing to see if enlisting aversion towards losses via the grading framework leads to better student performance. 

• Students were not informed when they signed up for their classes that they were part of a field experiment. 

• The loss framing (“counting down”) was associated with higher grades – some 2.6 to 4.2 percentage points higher. 

• Did students perform better in the loss framework simply because it was unusual? 

• A couple of related papers. not (yet?) covered by Behavioral Economics Outlines, are Roland G. Fryer, Jr, Steven D. Levitt, John List, and Sally Sadoff, “Enhancing the Efficacy of Teacher Incentives Through Framing: A Field Experiment," April 2018, pdf here) and Steven D. Levitt, John A. List, Susanne Neckermann, and Sally Sadoff, “The Behavioralist Goes to School: Leveraging Behavioral Economics to Improve Educational Performance,” American Economic Journal: Economic Policy 8(4): 183-219, November 2016. 

Larson, List, and Metcalfe (2016) on Myopic Loss Aversion and the Equity Premium Puzzle

Francis Larson, John A. List, and Robert D. Metcalfe, “Can Myopic Loss Aversion Explain the Equity Premium Puzzle? Evidence from a Natural Field Experiment with Professional Traders.” August 31, 2016; available here.

• The puzzle: the real return on US equities is about 8% per annum, versus about 1% for riskless assets. This spread cannot easily be explained as a risk premium. 

• One hypothesis: traders display myopic loss aversion (MLA), and hence the frequent downticks (short-term declines in asset value) are psychologically costly – people will only put up with these costs if there is an offsetting premium in the monetary return. If MLA can explain the equity premium puzzle, then it must be present in the “marginal” trader. 

• Laboratory experiments have found that myopic loss aversion is common. The standard design involves varying the rate at which price information is delivered to traders. Those who receive information at high frequency are exposed to more revelations of downticks, and hence, if they display MLA, they will underinvest in the risky asset, the one that is subject to lots of downticks. 

• The Larson, List, and Metcalfe paper employs a (natural?) field experiment, where traders do not know they are taking part in an experiment; they think they are beta-testing a new online trading platform. 

• The traders' recompense is to be paid eventually in-kind based on the profits that they accrue during their two weeks of testing. They can “buy” a risky asset whose return is tied (in a not-fully-obvious way) to the US dollar exchange rate. The tying is such as to bias the return to the asset to be positive. 

• The experiment reveals MLA – traders who are given infrequent (once per 4 hours) price updates keep more of their stake in the risky asset, and earn considerably more, than those traders who receive second-by-second updates. 

• Traders tend to desire more frequent price updates, but perhaps that information degrades their performance. 

• Since both the Frequent (n=73) and Infrequent (n=78) groups of traders can trade at any time, this experiment avoids a confounding feature of past laboratory experiments, that both information and trade opportunities are altered among conditions.

Winking and Mizer (2013) on a Field Experiment with the Dictator Game

Jeffrey Winking and Nicholas Mizer, “Natural-Field Dictator Game Shows No Altruistic Giving.” Evolution and Human Behavior 34(4): 288-293, July 2013.

• Laboratory experiments tend not to be fully anonymous, and the setting might also spur pro-social behavior; in other words, the external validity of lab experiments in questionable. [Recall Levitt and List (2007).]

• The authors run the dictator game – player one receives a windfall, and if he or she chooses, can split it with player two – in a field setting, where participants do not know that they are taking part in an experiment. In laboratory versions of the dictator game, almost 2/3 of dictators (player ones) offer some money, and the average offer is about 28% of the endowment. 

• The field version involves Confederate 1 waiting at a bus stop. The (involuntary, as it were) subject comes to the stop to wait for a bus. Confederate 1 moves off a bit to take a call, turning his back on the subject. Confederate 2 walks by quickly, on the phone, seems to notice casino chips in his pockets (three $5 chips and five $1 chips). Confederate 2 tells the subject that he is late for the airport, and offers him the chips. (In a second condition, Confederate 2 mentions that the subject could split the chips with Confederate 1.) Confederate 1 eventually sidles back after Confederate 2 has left, giving the subject an opportunity to split the chips. After 30 seconds, the experimenters reveal what they are up to, everyone enjoys a hearty laugh (I made that part up), and the subject completes a questionnaire for further payment. There is yet a third condition involving folks from the same bus stops playing an acknowledged dictator game experiment using casino chips. 

• In the field experiment, no one shared any chips. In the third condition (where the experiment was explicit), most subjects shared some chips, behaving in the standard laboratory fashion. 

• One possible confounding factor: it may be that the subjects usually would share the chips, but they just weren’t that keen on Confederate 1!

Maniadis, Tufano, and List (2014) on Anchoring Effects

Zacharias Maniadis, Fabio Tufano, and John A. List, “One Swallow Doesn’t Make a Summer: New Evidence on Anchoring Effects.” American Economic Review 104(1): 277–290, 2014 [pdf of earlier version here]. 

• A 2003 article by Ariely, Loewenstein, and Prelec found huge anchoring effects in the willingness-to-pay for goods and the willingness-to-accept payment for listening to aversive sounds. These experiments, along with others, undermine the usual economics assumption of fixed preferences. 

• Maniadis, Tufano, and List replicate parts of the earlier study and find some anchoring, but the effects are about ½ to ⅓ the size identified in the earlier article. 

 • The general conclusion on anchoring drawn by Maniadis, Tufano, and List: anchoring effects are real, but there is no evidence concerning their magnitude in economically important settings. 

• Beware of interesting new findings! Statistical significance means little in isolation. Be a Bayesian: if the prior probability of a result is small, do not rush to accept it on the basis of one published study. 

• The greater the number of independent researchers who are working on a specific finding, the lower the likelihood that a single publication identifying the finding is correct. 

• Research and other biases also can enter the picture; for instance, journals might systematically be less interested in publishing non-findings than (statistically significant) findings. 

• The replicability of a study is the key to inculcating rational belief. One or two independent replications tend to greatly add to the probability that a finding is correct. [It’s a movement!; see http://replicationnetwork.com/.]

• A potentially useful reference is Samuel Arbesman, The Half-Life of Facts: Why Everything We Know has an Expiration Date, Current, 2012.

On Varying the Stakes in Ultimatum Games (2011)

Steffen Andersen, Seda Ertaç, Uri Gneezy, Moshe Hoffman, and John A. List, “Stakes Matter in Ultimatum Games.” American Economic Review 101: 3427–3439, December 2011.

• A standard result is that varying the stakes does not lead to much of a change in the outcomes of ultimatum game (and related game) experiments. The ultimatum game is of interest in itself, but also because it seems to hold lessons for any “take-it-or-leave-it” bargaining situation. 

• Andersen et al. (2011) challenge this standard result. In particular, they hope to see if “proposers” offer more “unfair” splits when the stakes are high, and if responders turn down unfair splits, even when the stakes are significant.

• In the reported experiments, conducted in villages in India, the stakes are altered by a factor of 1000. The highest-stake version is on the order of one-year’s income. 

• The ultimatum game that the authors employ is structured in such a way as to nudge proposers into making “unfair” offers. Otherwise, the experimenters suspect that there will not be enough unfair offers to test reliably the willingness of responders to turn down unfair offers at high stakes. (The ultimatum game as it is typically implemented has its own share of nudge issues.) 

• In the experiments, raising the stakes monotonically decreases the average percentage of the pie “offered,” though the absolute monetary amount offered increases. At the highest stakes, there is but one rejection in 24 trials. Nevertheless, at the second-highest level of stakes (about one-month's income), more than one-quarter of the proposals are rejected.

• Is it ethical to go to relatively poor villages and offer some people the potential for one year's or one month's income -- along with the (likely) prospect that some of those selected people will proceed to "lose" that stake, after being nudged towards an "unfair" offer that raises the probability of their receiving nothing? Behavioral economics experiments sometimes challenge the Kantian precept that people are to be treated as ends in themselves, not means to the ends of others. 

Levitt and List (2007) on Laboratory Experiments

Steven D. Levitt and John A. List, “What Do Laboratory Experiments Measuring Social Preferences Reveal about the Real World?” Journal of Economic Perspectives 21(2): 153-174, Spring, 2007.

• Five laboratory games that reveal something about pro-social behavior: (1) the Ultimatum Game; (2) the Dictator Game; (3) the Trust Game; (4) the Gift Exchange Game (where the first player requests a level of “effort” from the second player -- pdf here); and (5) the Public Goods Game (good video here). In the real world, it can be hard to differentiate between pro-social preferences and sophisticated self-interest seeking. 

• Model notation: action choice a; wealth W; stakes (or value) v; moral cost M; social norms n; and scrutiny s. 

• The higher the negative financial externality an action imposes on others, the higher the moral cost M is taken to be. (Levitt and List also assume that this externality increases with the stakes v). M is higher the greater the deviation between action a and the social norm n. M also is raised by increased scrutiny s. 

• Individual utility is U(a, v, n, s) = M(a, v, n, s) + W(a, v). Higher stakes v can raise W while raising M, too, but the authors assume that W rises more quickly with v. (Another interpretation might be that the norm changes with v, so that selfish behavior receives more social imprimatur.) 

• Scrutiny is different and typically more intense in the lab, exaggerating pro-social behaviors. (Alternatively, scrutiny from one’s children or other family members has no lab parallel.) Further, lab participants might believe that an experiment demands some pro-social behavior. 

• Behavior might be sensitive to factors that unavoidably vary between the lab and the real world: the experimenter cannot fully control the context. Participants bring context with them, and hence are playing a different game. 

• Lab participants self-select, directly or indirectly, while market participants self-select, too.

Heffetz and List (2014) on Reference Points and Endowments

Heffetz, Ori and John A. List, “Is the Endowment Effect an Expectations Effect?” Journal of the European Economic Association 12(5): 1396-1422, October 2014.

• Three experiments are conducted to test the Koszegi and Rabin (2006) version of prospect theory, in which the reference point consists of recent expectations for future consumption. In part, Koszegi and Rabin were motivated by List’s evidence that endowment effects dissipate with market experience. 

• A pared-down description of the experimental set-up: Subjects flip a coin to determine whether they are assigned a mug or a pen. After this assignment, in the Strong Expectations condition, they are told that there is a 99% chance that the good (mug or pen) that they were assigned by the coin flip is what they have to keep, but there is a 1% chance they will be allowed to trade for the other item. (That is, Strong Expectations means that you virtually own the good that was randomly assigned.) In the Weak Expectations condition, the probability is reversed, so the assignment is very unlikely to be binding. Then (eventually), subjects have to choose which good they want. Only after that do they learn whether their choice matters, or whether the realization of the randomization dictated that they had to stick with their assignment. 

• The Koszegi and Rabin model suggests that under Strong Expectations, the coin-flip assignment should affect preferences – but not under Weak Expectations. What Heffetz and List found, however, is that the assignment matters a lot, with no difference between the Expectation conditions. 

• Experiments by Marzilli Ericson and Fuster, alternatively, found a big effect of strong v. weak expectations in a different experimental set-up. Heffetz and List run two experiments similar to those of Marzilli Ericson and Fuster, but do not replicate their results. Instead, Heffetz and List basically continue to find that the random assignment matters, and that the Expectations condition has no effect – contrary to Koszegi and Rabin and to Marzilli Ericson and Fuster.

John List (2004) on the Endowment Effect

John A. List, “Neoclassical Theory Versus Prospect Theory: Evidence from the Marketplace.” Econometrica 72: 615–625, 2004.

• Subjects start with one of four endowments: mug; chocolate bar; both; or, neither. Note that mugs and chocolate bars are common, everyday items.

• Subjects are offered the opportunity to trade for the other good (in the mug or chocolate conditions) or forced to trade their endowment for just one of the goods (both condition) or get to choose either the mug or chocolate (none condition). 

 • Non-dealers were about four times more likely to leave with the endowed good than with the other good. Dealers, though, betray almost no sign of an endowment effect. Further, for non-dealers, more trading experience reduces the endowment effect. 

 • Note that “trading experience” refers to trading background for goods unconnected to chocolate bars or mugs.