Understanding and Curing Myopic Voting

Gabriel S. Lenz Massachusetts Institute of Technology

glenz@mit.edu

November 2, 2010

Preliminary draft

Retrospective voting is central to theorizing about democracy. Given voters’ ignorance about politics and public policy, some argue that it is democracy's best defense. This defense, however, assumes citizens are competent evaluators of incumbent politicians' performance. Although little research has investigated this assumption, voters' retrospective assessments in a key domain, the economy, appear flawed. They overweight election-year income growth in presidential elections, ignoring cumulative growth under the incumbent. In this paper, I present evidence that this myopia arises from a more general “end bias” in retrospective assessments. Using a three-year panel survey, I show that citizens' memories of the past economy are inconsistent with their actual experience of the economy as they reported it in earlier interviews. They fail to remember the past correctly in part because the present shapes their perceptions of the past. I then show similar behavior in the lab. When participants evaluate economic and crime data, I again find that election-year performance shapes perceptions of overall performance, even under conditions where the election year should not be more informative. Finally, I search for and appear to find a cure. Presenting participants with cumulative information on performance (e.g., total income growth or total rise in murders during incumbents’ terms) cures this myopia. On one hand, these results are troubling for democracy because they confirm citizens’ incompetence at retrospection. On the other hand, they point to a remedy, one that candidates and the news media could adopt.

I thank Eitan Hersh, Paco Flores-Macias, Mike Myers, and Michael Peress for helpful comments and suggestions, as well as seminar participants at MIT and Yale University.

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The first systematic investigations of citizens' knowledge about politics revealed a bleak

picture (Berelson, Lazarsfeld, and McPhee 1954; Campbell et al. 1960). In their landmark study, Berelson, Lazarsfeld, and McPhee (1954), for instance, assessed citizens' awareness of the two most prominent public policy issues in the 1948 presidential election campaign, issues on which Truman and Dewey, the Democratic and Republican presidential candidates, disagreed. These issues were government policy towards labor unions (Taft-Hartley) and price controls. According to Lazarsfeld and his colleagues, Truman's and Dewey's differences on these two issues were “reasonably straightforward and clear” and were “crucial issues in the campaign, much discussed in the communication media” (Berelson, Lazarsfeld, and McPhee 1954, 227-28). Nonetheless, their survey found a pervasive ignorance about Truman's and Dewey's positions: only 16 percent of their sample knew both candidates' positions on both issues.

Numerous studies have confirmed this lack of political knowledge among the public (Delli Carpini and Keeter 1996; Zaller 1992). To provide a more recent example, only 55 percent of citizens in 2004 saw Kerry and the Democratic Party as more supportive of abortion rights than they saw Bush and the Republican Party, a percentage probably inflated by guessing.1

Given voter ignorance, researchers turned to retrospective voting as an explanation for democracy's success (Fiorina 1981; Key 1968; Kramer 1971). Democracy may work despite this ignorance, these scholars argued, because citizens can judge politicians retrospectively on their performance. They can simply ask, are we better off than we were four years ago? Are we losing a war? Has our standing in the world improved?

This retrospective solution to the democratic dilemma, however, assumes citizens are competent evaluators of performance. Although little research has investigated this assumption, evidence suggests that, at least on the economy, voters' assessments are flawed. They appear to judge incumbents myopically, focusing mostly on election-year income growth, not cumulative growth. Numerous studies have documented the importance of election-year income growth (e.g., Kramer 1971), though interpreting it as myopic is recent (Achen and Bartels 2004; Bartels 2008). Presidents, the data indicate, can preside over poor economic conditions for much of their terms and still win reelection, as long as the economy grows in the months before Election Day.

The myopic tendencies of citizens have profound implications for public policy. Most importantly, they create perverse incentives for presidents. To increase their chances of winning reelection, they may boost economic growth during election years, even at the cost of future growth. As Tufte (1978) writes, voters' short time horizons could produce “a bias toward policies with immediate, highly visible benefits and deferred, hidden costs ─ myopic policies for myopic voters.” Evidence suggests that presidents enact precisely these sorts of policies with observable consequences: on average, real disposable income growth (RDI) is significantly higher during presidential election years (Achen and Bartels 2004; Bartels 2008).2 By focusing on the election-year economy, voters may reelect presidents most willing to manipulate the economy (adverse selection), such as Richard Nixon (Tufte 1978), while suffering from the deadweight loss induced by wasteful government spending.

1 2004 American National Election Study. 2 Although evidence for political business cycles is mixed (Nordhaus 1975; Schultz 1995), the evidence in

the U.S. and in Latin America appears stronger (Nieto-Parra and Santiso 2009; Streb and Lema 2009). Moreover, as Achen and Bartels (2004) point out, most studies do not test for cycles with the variable most likely to be manipulated: income growth, especially real disposable income growth, which accounts for taxes, transfers, and inflation.

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In this paper, I present evidence that myopic economic voting arises from a more general “end bias” in retrospective assessments, one that psychologists have documented in other domains (Ariely and Carmon 2000; Redelmeier and Kahneman 1996; Varey and Kahneman 1992). When citizens attempt to assess incumbent performance, their experiences at the end of terms appear to shape their memories of earlier performance. To support this claim, I present findings from panel surveys and experiments. Using panel data, I show that citizens' memories of the past economy are inconsistent with their actual experiences as they reported them in earlier interviews. They fail to remember the past correctly in part because the present shapes their perceptions of the past. In several experiments where participants evaluated hypothetical and real economic and crime data, I find the same end bias. Finally, I search for and appear to find a cure. Presenting participants with cumulative information on performance (e.g., total income growth or total rise in murders during incumbents’ terms) cures them of their myopia.

These results raise further concerns with retrospective voting as a defense of democracy, suggesting that citizens’ evaluations of incumbents may be flawed in domains other than just the economy. On the other hand, however, they point to a remedy, one that candidates and the news media could adopt.

Remembered versus experienced utility: end bias In its simplest form, retrospective voting should be easy. As Fiorina (1981, 5) puts it,

“[Citizens] need not know the precise economic or foreign policies of the incumbent administration in order to see or feel the results of those policies. . . . In order to ascertain whether the incumbents have performed poorly or well, citizens need only calculate the changes in their own welfare.” Surprisingly, however, findings from psychology indicate that people often get these calculations wrong. The utility people experience in fact often diverges considerably from the utility they remember afterwards (Kahneman, Wakker, and Sarin 1997).

Instead of remembering overall utility, people attend to certain attributes, such as the peak pleasure or pain experienced, and neglect other attributes, such as duration (Ariely and Carmon 2000; Redelmeier and Kahneman 1996; Varey and Kahneman 1992). Of all the attributes, people most consistently attend to the end of experiences. Consider, for example, four dental treatments spaced over a week in which the intensity of pain either increases {2, 3, 4, 5} or decreases {5, 4, 3, 2}. Although individuals experienced the same total discomfort, retrospectively, they would remember the decreasing sequence as much less painful.

A series of experiments conducted by Varey and Kahneman (1992) provide a good example of this research. Participants began the studies by immersing one hand in very cold water for ten seconds. They were then told to expect three more trials of this kind, but only two were actually conducted. In the Short trial, participants kept one hand in water at 14°C for 60 seconds. In the Long trial the immersion lasted 90 seconds. Water temperature was kept at 14°C for the first 60 seconds, at which point the experimenter gradually raised the temperature from 14°C to 15°C over the next 30 seconds (unbeknownst to the participants). Half the participants experienced the Short trial before the Long one; the sequence was reversed for the other participants. After a seven minute delay, participants were called in for a third trial, informed that they would repeat one of the two previous procedures, given a choice of whether the first or the second trial should be repeated, and asked to answer several questions about the first two trials. Kahneman and his collaborators conducted several studies with this general design.

The results of these studies are striking. Even though participants experienced more total pain in the Long trial, they generally remembered it as less painful, and a large majority

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preferred to repeat the Long trial. The ever so slight decrease in pain experienced in the last 30 seconds of the Long trial led participants to remember it as less painful.

According to the researchers, post-experimental interviews and other observations provided no support for alternative explanations, such as a desire on the part of participants to endure more pain, experiencing the last segment of the Long trial as pleasurable (or not painful), experiencing the Long trial’s post-immersion as more pleasurable, or failing to remember its longer duration (most participants could correctly answer a question about the durations of the two trials). When they asked participants, in a separate study, to choose between hypothetical profiles of a Long and Short trial, participants invariably choose the Short trial.3

Numerous studies document similar phenomena across a wide range of domains, including monetary payments (Loewenstein and Sicherman 1991), life experiences such as vacations (Loewenstein and Prelec 1991; Loewenstein and Prelec 1993), emotional episodes (Fredrickson and Kahneman 1993; Varey and Kahneman 1992), TV advertisements (Baumgartner, Sujan, and Padgett 1997), queuing experiences (Carmon and Kahneman 1996), pain (Ariely 1998; Ariely and Carmon 2000; Varey and Kahneman 1992), discomfort (Ariely and Zauberman 2000; Kahneman et al. 1993; Schreiber and Kahneman 2000), medical outcomes and treatments (Chapman 2000; Redelmeier and Kahneman 1996), gambling (Ross and Simonson 2006), and academic performance (Hsee, Abelson, and Salovey 1991; Zauberman, Diehl, and Ariely 2006).

The end of an experience not only shapes perceptions among those undergoing the experience, but also among observers, who exhibit the same biases. For example, in a study of colonoscopy patients, Redelmeier and Kahneman (1996) found that the peak pain and the pain experienced at the end of the procedure best predicted retrospective evaluations of colonoscopies’ painfulness, while the total pain experienced did not. After the procedures, researchers asked the administering physicians to rate each patients' overall discomfort. The physicians’ ratings evinced the same biases as the patients. Moreover, when asked which patients should have received more anesthetic, the doctors answered, not based on total pain, but on the peak and the end.

Observers also do not have to directly observe the experience to exhibit these biases. Varey and Kahneman (1992), for example, presented participants with a booklet containing discomfort ratings allegedly experienced by individuals as they underwent unpleasant experiences, such as listening to loud drilling noises. The booklet’s discomfort ratings, shown on a 10-point scale, differed in duration and in intensity over time, with each page showing a separate experience. After looking through the booklet, participants provided a global evaluation of each experience on a 0-100 scale. Even though participants did not directly observe the unpleasant episodes, they based their global evaluations primarily on the maximum and final intensities, with little weight on duration. For instance, participants rated the overall pain in the pain sequence {2, 5, 8} as worse than the overall pain in the sequence {2, 5, 8, 4), where larger numbers indicate more intense pain and each number represents the discomfort felt over a five-minute period. Based on these and other studies, observers thus appear to share the same biases in retrospective evaluations as those undergoing experiences. In particular, they both overweight the end.

Although coldwater immersion, colonoscopies, and loud drilling noises seem far afield from politicians’ performance, these studies suggest general biases in retrospection, especially

3 They did not do so, however, when judging hypothetical experience profiles one by one, only one they

had to choose between them.

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end bias. Moreover, several studies find similar behavior in domains that more closely resemble politicians’ performance, such as evaluating factories’ production of defective products (reject rate) or tests of ability (Zauberman, Diehl, and Ariely 2006).

No consensus exists about the mechanism behind these biases, nor has much research investigated it. Nevertheless, these biases are consistent with a mechanism called attribute substitution (Kahneman 2003; Kahneman and Frederick 2002). When people attempt to judge a target attribute, such as the change in their welfare under an incumbent president, they search for a reasonable value. For some judgments, this search terminates almost immediately because the required value is readily accessible (e.g., the question “How old are you?”). For many judgments, however, the target attribute does not readily come to mind, but the search for it evokes other attributes that are related, such as “has my welfare improved this year.”4 People then automatically substitute these related attributes for the target attribute. Given people's limited cognitive capacity and limited interest in politics, attribute substitution seems likely to occur when evaluating politicians’ performance.

Alternative explanations and diagnoses A cognitive bias is, of course, not the only explanation for myopic economic voting. I

briefly review two alternative explanations. An obvious one is that the last-year of incumbents' terms may be (or may seem) more informative. Since policies may take time to have their full effect, the last year may reveal the most about the incumbents' quality and may provide the best forecasts of second-term performance. Several facts, however, suggest that this explanation is either wrong or, if correct, the behavior itself is not optimal. In particular, the election-year economy does not in fact forecast the economy of the following four years when incumbents are retained (Achen and Bartels 2004).5 Voters may, nevertheless, reasonably think that the fourth-year is more informative even if it is not. As I show below, however, survey and experimental evidence suggests they don't.

Another alternative arises from modeling of principle actor interactions. At times, principals (voters) may desire to incentivize actors (incumbents) to exert effort in the last period of multi-period game by committing to reward them if they do, even if the actors shirk in early periods. Bueno de Mesquita and Landa (2007) describe this as “What Have You Done For Me Lately” behavior. Although this should be explored further, it's not clear that citizens see an incumbent president’s four-year term as a multi-period game, at least with respect to the economy.

4 According to Kahneman and Frederick (2002, 54), attribute substitution occurs when the target attribute is

assessed by substituting the value of another attribute on the target when three conditions are satisfied: “(1) the target attribute is relatively inaccessible; (2) a semantically and associatively related candidate attribute is highly accessible; and (3) the substitution of the heuristic attribute in the judgment is not rejected by the critical operations of System 2.” Where System 2 refers to reflective cognitive processes, which are controlled, effortful, deductive, slow, and rule-based. System 1 refers to intuitive cognitive processes, which are automatic, effortless, and associative.

5 In general, RDI growth does not predict future RDI growth. In the post-World War II economy, for example, last year's RDI growth doesn't predict next year's. Regressing percent RDI change on lagged percent RDI change yields a coefficient of .11 with a standard error of .12, standard error of regression of 2.1, and an R2 of .01.

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(Mis)Remembering your prior economic perceptions President George H. W. Bush presided over a weak economy from late 1990 through

until he faced reelection in 1992. In the three waves of the American National Election Study (ANES) Panel that cover this period (1990, 1991, and 1992), the percent seeing the economy as having gotten somewhat worse or much worse was 77 percent in 1990, 65 in 1991, and 72 in 1992. At the end of this panel (1992), the ANES did something rare. It asked about the economy over a period longer than a year. In addition to the usual one-year question, it asked about the previous four years. The exact wording was, “Compared to four years ago, would you say that the nation's economy has gotten [much/somewhat] better, stayed about the same, or gotten [much/somewhat] worse?”

When people answered this question, did they actually consider what happened in earlier years? Or, did the end, in this case, 1992, shape their prior four-year retrospective evaluations? Since these responses were part of a panel survey, we can test whether people ignored their 1990 and 1991 perceptions, and primarily relied on their 1992 perceptions when answering the four-year question.

To measure economic perceptions in each year, the ANES question asks, “Has the nation's economy gotten [much/somewhat] better or [much/somewhat] worse or stayed the same in the past year?” For the analysis, I rescale all the variables to vary between 0 and 1. Table 1 presents the means and standard deviations of these variables.

Figure 1 provides suggestive evidence that people did focus more on 1992. It plots the average response to the four-year question against responses to the one-year questions in 1990, 1991, and 1992. The slope for 1992 is .49, about 150% larger than the slopes for 1990 and 1991, which are about .30.

People’s views about the economy in each year are probably correlated, making it difficult to know which year actually matters. To address this, I regress four-year evaluations on one-year evaluations. As Table 2 shows, the results even more clearly reveal the extent to which people either forget or down weight their responses in earlier years. The coefficients are .16, .12, and .43, for 1990-1992, respectively, which means 1992 receives about 300% more weight than the earlier years.

Moreover, these results do not appear to arise because of a general anti-Bush sentiment or partisanship that pervades responses in 1992. As the next column in Table 2 shows, the results hold when I control for party identification, Bush approval, an employed indicator, household income, married, education, political knowledge, and male, all measured in 1992. They also hold among just Democrats, just Republicans, and just independents (not shown). In short, these findings are consistent with end bias in retrospective evaluations of the economy, much like that shown in psychology studies.

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Table 1: Average perceptions of the prior-year and four-year economies in the 1990-91-92 ANES Panel

slope = .30 slope = .30

slope = .49

0

.2

.4

.6

0

.2

.4

.6

0 .5 1

0 .5 1

1990 1991

1992

Four

-yea

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nom

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Economic evaluations (in respective year)

Figure 1: When retrospectively evaluating the four-year economy in 1992, participants place more weight on 1992 This figure shows the average response to the four-year question against responses to the one-year questions in 1990, 1991, and 1992. The slope for 1992 is .49, about 150% larger than the slopes for 1990 and 1991, which are about .30.

Variable Mean SD Economic perceptions 1990 .24 .19 Economic perceptions 1991 .29 .21 Economic perceptions 1992 .23 .22 Economic perceptions 1988-1992 .18 .21

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Table 2: When retrospectively evaluating the four-year economy in 1992, participants place more weight on 1992

DV: Economic perceptions 1988-1992 (1) (2) (3) (4) (5) Economic perceptions 1990 0.30*** 0.16*** 0.13*** (0.036) (0.034) (0.033) Economic perceptions 1991 0.28*** 0.12*** 0.080*** (0.032) (0.031) (0.031) Economic perceptions 1992 0.49*** 0.43*** 0.38*** (0.029) (0.029) (0.031) ( )Constant 0.11*** 0.10*** 0.071*** 0.013 0.092*** (0.011) (0.012) (0.0092) (0.012) (0.031) Observations 893 893 893 893 893 R-squared 0.074 0.078 0.245 0.287 0.337 SER 0.21 0.21 0.19 0.19 0.18 Standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1. All variables coded to vary between 0 and 1.

Additional control variables X

Column 5 includes the following additional controls (measured in 1992): PID, Bush approval, Unemployed indicator, Household income, Married, Education, Political knowledge, and Male.

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Myopia also afflicts observers If the end bias that psychologists have observed in other domains lies behind election-

year retrospective economic voting, it should occur equally among people who actually experienced these economies and among observers. In this section, I test this prediction. I present the results of a series of studies where I showed participants economic and crime data. The experiments all had a similar design, one resembling psychology studies about end bias. In each, I showed participants bar plots of the yearly percent change in income or crime in each year of incumbents’ four-year terms. Participants saw between 15 and 25 such plots, each showing a four-year term, with the order of the terms randomized for each subject. In some of the studies, I generated the income and crime growth data by randomly drawing them from a normal distribution with a mean and variance chosen to match real-world data. In others, I use data from the historical record. Figure 2 presents two examples of these plots drawn from one study of the randomly drawn sort. In the first, the economy ends on a high note. In the second, it does not. Before showing the plots, participants read instructions that, in the economic cases, briefly explained income growth, mentioning that it was a good measure of the overall strength of the economy during a president's term, and noting that these data are either real or hypothetical. Below each plot, I asked them to evaluate the economy during the period shown. I recruited participants through a web service, paying them $.15-$.25.6 Before analyzing the data, I drop participants who fail to evaluate each term and who fail a simple test of attention to the English instructions, usually about 10% of the samples.

End bias with randomly generated income growth — 2nd term presidents In the first study, I showed participants 25 plots, with each displaying yearly income

growth for a hypothetical presidents’ four-year term. To ensure that participants do not weight up later years because of beliefs about policy lags — first term presidents’ policies taking some time to kick in — I told participants that the plots showed economies under second term presidents.7 I generated the yearly income growth data from a normal distribution with a mean and standard deviation equal to two, which is the average in the actual income data from 1947-2008. Below each plot, I asked, “How would you rate the condition of the national economy during this period? Is it very good, fairly good, fairly bad, or very bad?” To put income growth and these evaluations on a similar scale, I recoded responses to vary from 0 to 10, with 10 corresponding to “very good.” I take the average of the responses for each of the 25 terms and call this variable Economic evaluations.

Even though they are not directly experiencing these economies, and even with all four years in front of them, did participants still exhibit end bias in their retrospective evaluations? Figure 3 shows that they did. It plots participants’ average evaluation of the economy during the

6 I recruited subjects through Amazon.com's Mechanical Turk service (www.mturk.com). This service

allows researchers to recruit and pay subjects for participating in web-based studies. Although initially set up by Amazon.com to undertake tasks only humans could readily complete, such as recognizing products in pictures, it has expanded and people now post jobs of numerous sorts, including social science experiments. Research suggests that people do these tasks for little pay because they are bored at their jobs. Most tasks pay between 5 and 50 cents. To collect the ratings, we use an online survey service called Survey Gizmo (www.sgizmo.com).

7 To check whether subjects read and remembered these instructions, I asked them at the end of the study whether these hypothetical presidents were in their first terms, second terms, or third terms. Of the 64 respondents, only five answer this incorrectly. The results are identical when I exclude these five from the analysis.

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four-year periods against each year’s randomly generated income growth. When participants evaluate the economy, the figure shows, they pay almost no attention to growth in the first year (note the slightly negative slope), some weight to the second year, which has a positive slope, and considerable weight to the third and fourth years, with the fourth-year having the steepest positive slope and tightest fit. The fourth year slope is significantly larger than the third year or earlier years (ps <.01). So, even with all four years in front of them and even though they were told these were for a second term presidents, end bias emerges.

Figure 2: Examples of two plots shown to participants Even though average income growth is higher in the economy shown in the bottom plot, 2.85%, than in the top plot, 2.60%, participants rated the economy on the top as stronger. On the 10-point scale, they rated the top as 9.1 on average and the bottom as only 6.3.

10

0

5

10

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5

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-5 0 5 10 -5 0 5 10

Year 1 Year 2

Year 3 Year 4

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Income growth % in each respective year (simulated)

Figure 3: When evaluating the simulated four-year terms, participants focus more on the fourth year

To further explore these patterns, Table 3 presents regression estimates. In the first

column, I regress the average evaluation on the income growth in each of the four years.8 Controlling for income growth in each year changes the pattern of the coefficients slightly from that shown in Figure 3 (because of chance correlations between yearly growth), but the overall pattern remains the same. Participants place several times more weight on the last year (b = .61) than on the first year (b = .28) and all the estimates are statistically significant.

Participants’ retrospective evaluations of the plots in Figure 2 (page 9) illustrate this behavior. They rated the economy shown on the top of Figure 2, which ended well with 4.4% growth, as considerably better than the one at the bottom, which ended on a weak note, with only 1.7% growth. On the 10-point scale, they gave the figure on top an average of 9.1, but the bottom figure only 6.3. They did so even though the top figure has a higher overall average growth rate, 2.85% versus 2.60%, which is plainly visible to the eye.

The end bias findings on the economy appear robust. The results held when I reran the study with all aspects the same except I did not label the terms as second term (see Column 2, Table 3). They also held in additional studies with new sets of randomly drawn income data (see Column 3 and 4, Table 3). The final column of Table 3 presents the (precision weighted) average of all the studies. It shows that, on average, people place to 270% more weight on the fourth year than on the first year, and 155% more weight on the fourth-year than the third year. Both differences are highly statistically significant.

8 I also examined these data at the individual level using ordered probit and clustering the standard errors at

the individual level or the term level. The results were essentially the same.

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Table 3: When evaluating hypothetical income growth during four-year terms, participants exhibit end bias Simulated economic data (25 four-year terms). Dependent variable: How would you rate the condition of the [national economy or state economy] during this period? Is it very good, fairly good, fairly bad, or very bad? To put income growth and these evaluations on a similar scale, I recoded responses to vary from 0 to 10, with 10 corresponding to “very good.” I take the average of the responses for each of the 25 terms, so the N for the regressions is 25 (a conservative approach to analysis). The precision weighted column average includes the studies from Columns 1-4 and from Table 7, Column 1.

Replication (1) (2) (3) (4) (5)

DV: Four-year economic evaluations Randomly drawn

income data Same data

as (1) Another random

draw

Another random draw

Average (precision weighted)

Office President President President Governor All Term Second Not specified All

Income growth % Year 1 0.28*** 0.22** 0.30*** 0.11 0.23*** (0.097) (0.083) (0.038) (0.080) (0.027) Year 2 0.47*** 0.39*** 0.25*** 0.26*** 0.39*** (0.081) (0.078) (0.055) (0.073) (0.035) Year 3 0.37*** 0.31*** 0.45*** 0.40*** 0.40*** (0.066) (0.060) (0.058) (0.10) (0.029) Year 4 0.61*** 0.66*** 0.59*** 0.69*** 0.62*** (0.058) (0.058) (0.047) (0.066) (.023) N (terms) 25 25 25 25 R-squared 0.926 0.923 0.924 0.889 SER 0.65 0.65 0.48 0.72 N (participants) 64 47 68 74 307 % weight on 4th year over 1st year

217%*** 300%*** 197%*** 627%*** 270%***

% weight on 4th year over 3rd year

165%*** 212%*** 131%*** 173%*** 155%***

Standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1.

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End bias with retrospective evaluations of crime prevention To see whether these results generalize to other domains, I replicated the second term

experiment with murder rates. I followed the same procedures except I labeled the axes as percent change in murders committed and told participants that these were hypothetical second term governors, not presidents. Participants saw 25 terms and the murder growth rates were drawn from a normal distribution with a mean and standard deviation equal to two. Figure 4 presents an example of one of these plots.

Instead of asking respondents about the economy, I asked, “How would you rate this governor's crime prevention record during this period? Is it very good, fairly good, fairly bad, or very bad?” To put murder growth and these evaluations on a similar scale, I recoded responses to vary from 0 to 10, with 10 corresponding to “very bad.” I then take the average of the responses for each of the 25 terms.

Table 4 regresses the average evaluation on each year's murder growth rate. Once again, end bias is evident. In fact, results are somewhat stronger than for income growth. Participants place many times more weight on the last year (b = .76) than on the second year (b = .12) or first year (b = -.05).

Figure 4: Example from murder rate experiment

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Table 4: When evaluating hypothetical murder rate changes during the four-year terms, participants exhibit end bias Simulated murder data (25 four-year terms). Dependent variable: How would you rate this governor's crime prevention record during this period? Is it very good, fairly good, fairly bad, or very bad? Is it very good, fairly good, fairly bad, or very bad? To put murder growth and these evaluations on a similar scale, I recoded responses to vary from 0 to 10, with 10 corresponding to “very bad” I take the average of the responses for each of the 25 terms.

(1)

DV: Four-year crime prevention evaluationsRandomly drawn

murder data Murder % change Year 1 -0.050 (0.068) Year 2 0.12** (0.054) Year 3 0.35*** (0.062) Year 4 0.76*** (0.069) N (terms) 25 R-squared 0.912 SER 0.60 N (participants) 36 Standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1

End bias with retrospective evaluations of real-world income data In this section, I show that people are equally myopic when viewing real-world income

data from presidents’ actual terms, instead of simulated data. Moreover, their myopia closely resembles voters’ actual response to this income growth in the 1944-2008 elections, a finding that adds external validity to these lab-like studies.

Before describing and presenting the real-world studies, I first show voters’ actual response to income growth in 1944-2008 presidential elections.9 In the first column of Table 5, I regress the incumbent party's popular vote margin on income growth in each year of the four-year terms. This regression provides us with a baseline against which we can compare participants’ behavior. Consistent with previous work, the election-year economy (Year 4) has a pronounced and statistically significant effect on voting (b = 4.37, p <.01). Each percentage point of election-year income growth increases the incumbent party’s expected margin by 4.4 percentage points. In contrast, third year growth has a much smaller effect (b = 1.48), which is not statistically significant at conventional levels. First and second year growth are slightly negatively related to vote margin, but essentially just zero. For whatever reason, citizens, mostly neglect all but the final year economy.

9 Income data from the early 1940s are from http://www.census.gov/prod/www/abs/statab.html.

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Do observers behave equally myopically with real-world data? Do they behave like citizens? To see whether they do, I showed participants yearly income growth for these 17 terms, the same data used in the vote-margin regression. I again presented these as hypothetical presidents in their second terms. Below each plot, I once more asked, “How would you rate the condition of the national economy during this period? Is it very good, fairly good, fairly bad, or very bad?” I again recode responses to vary from 0 to 10, with 10 corresponding to “very good,” take the average response to each of the 17 terms, and call this variable Economic evaluations.

When presented with the real-world data, people responded in the now familiar myopic pattern. Column 2 regresses Economic evaluations on income growth in each year. The pattern of coefficients closely resembles those for the simulated data. More importantly, the pattern resembles that for actual vote share in these elections. Since the incumbent vote share margin (the Column 1 DV) and Economic evaluations (the Column 2 DV) are on different scales, the similarity is not as clear as it could be. To address this, Columns 3 and 4 present the same regressions after recoding both DVs to vary between 0 and 1. Once recoded, this similarity is obvious. Fourth year income growth, for instance, has effect of .13 on Incumbent vote margin and .12 on Economic evaluations. Participants thus place less and less weight on earlier year's income growth, as do voters, with the first year being slightly negatively related to Economic evaluations, as it is for voters as well.

Given that real-world voters and lab participants respond so similarly to the same data, lab participants’ evaluations of the economy should predict actual voting quite well. Figure 5 shows that they do. It plots the incumbent party's popular vote margin against the average of valuation of the economy. Even though they thought these were hypothetical, second-term presidents, they nevertheless predict the actual election margins with surprising accuracy. By showing that observers exhibit the same behavior as voters, these findings further support the end-bias explanation for myopic economic voting.

Of course, people's focus on election-year income growth in the lab could arise for reasons having nothing to do what with why voters focus on election-year income growth in the real-world. In particular, the focus on the final year could be simple laziness. People may rush through the plots and only remember what they saw last, which might be fourth year growth. To address this alternative, I conducted an experiment where I displayed the income growth with horizontal bars, instead of vertical bars. The study had two conditions. In the normal condition, the bars were in descending order, with Year 1 at the top and Year 4 at the bottom. In the reversed condition, I flipped the bars, so participants saw Year 4 at the top and Year 1 at the bottom. Figure 6 presents examples of these plots. If the lab myopia reflected merely a visual error, the myopia should disappear (or reverse) in the reversed condition. As the right two columns of Table 5 show, however, the myopic pattern shows up in both conditions.

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Table 5: Participants respond to plots of real-world income data in the same way voters do to actual income growth 1941-2008

17 four-year presidential terms (subjects told these were hypothetical, 2nd-term pres.)

Replication 1949-2008

15 four-year terms (1) (2) (3) (4) (5) (6)

DVs rescaled 0 and 1 Horizontal

bars Horizontal reversed

DV: Actual inc. vote margin

Econ. eval.

Inc. vote margin

Econ. eval. Econ. eval.

Income growth % Year 1 -0.032 -0.065 -0.00093 -0.0098 0.16*** 0.19*** (0.70) (0.063) (0.021) (0.0095) (0.028) (0.039) Year 2 -0.43 0.24*** -0.013 0.036*** 0.29*** 0.34*** (0.70) (0.063) (0.021) (0.0095) (0.033) (0.039) Year 3 1.48 0.47*** 0.044 0.071*** 0.17*** 0.17*** (0.94) (0.084) (0.028) (0.013) (0.034) (0.053) Year 4 4.37*** 0.77*** 0.13*** 0.12*** 0.48*** 0.50*** (1.07) (0.096) (0.032) (0.015) (0.060) (0.072) N (terms) 17 17 17 17 15 15 R-squared 0.640 0.916 0.640 0.916 0.949 0.933 SER 7.32 0.66 0.22 0.099 0.052 0.063 N (participants) NA 64 NA 64 Standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1

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Figure 5: Participants’ evaluations of the yearly income growth predicts the election margins of actual presidential elections with surprising accuracy

Figure 6: Examples of plots from the horizontal-bar vs. horizontal-reversed experiment

Horizontal-bar condition Horizontal-reversed

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Further evidence that it's not because the fourth year is more informative

As noted above, an alternative explanation for myopic retrospective economic voting is that participants believe later years are more informative about the presidents’ performance. Several facts, however, suggests that this interpretation is unlikely. First, similar patterns show up in numerous psychology studies even when the end is not more informative, such as in the cold water trials or in observers’ evaluations of other people's experience listening to loud drilling noises (Varey and Kahneman 1992).

Second, in economic cases, the evaluation question used in the studies above asked, not about the presidents’ performance, but about “the conditions of the national economy during this period?” So, a literal reading of the question should not elicit considerations about policy lags (though the context may have triggered them).

Third, participants are apparently unaware of the extent to which they upweight later years. Right after participants rated the four-year periods in the second-term, simulated income study, I asked them, “When evaluating the economy during these four-year periods, how much weight did you give to each year?” I then instructed participants to record a percent for each year with the total summing to 100% (the survey showed respondents the sum as they entered the weights). As Table 6 shows, participants report giving each year roughly equal weight, though the averages do increase a bit: 19.3%, 23.2%, 28.4%, and 29.5%, for the first through fourth years, respectively. Compared to the greater attention actually given to later years, these differences are small. Participants only report placing about (29.5%/19.3%/ =) 50% more weight on the fourth year relative to the first year, but they actually place (.62/.23*100 =) 270% more, based on the average of the simulated-data studies (see Table 3). Of course, these weights are not necessarily comparable, but the differences still seem striking. I have rerun this question several times, finding the same results.

To further test whether respondents down weight earlier years because of policy lags, I conducted another study in which participants evaluated simulated income growth data over much longer periods. I randomly assigned participants to see two versions of the 25 yearly-income-growth plots. In a four-year condition, respondents saw plots just like those shown above, except I told them that the plots showed yearly income growth in a state for a hypothetical governor’s term, instead of a hypothetical president’s term.10 In the four-term condition, I told participants that the plots showed the average income growth in each term for governors with especially long tenures: four terms, each of four years. I left the plots exactly the same except I retitled them and relabeled the four income growth bars, not as years 1-4, but as terms 1-4. (See Appendix for examples.) If a basic cognitive bias gives rise to myopia, I expect participants to weight up later terms as much as they up weight up later years. Of course, up weighting later terms could be reasonable, assuming very long policy lags, but up weighting them to the same extent that they up weight later years in a four-year term seems unreasonable. As expected, participants behave equally myopically with four-terms as they do with four years. The Appendix presents the results. In short, this experiment provides yet further evidence that myopia reflects a cognitive bias, not a deliberate strategy.

10 In retrospect, I probably should have told subjects that the four-year plots showed governors in their

second terms.

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Table 6: Self-reported weights on income growth When evaluating the economy during these four-year periods, how much weight did you give to each year? (Please enter a percent for each year, with the total summing to 100%.) Means Medians Year 1 19.3 20 (0.87) (1.46) Year 2 23.9 25 (0.95) (0.97) Year 3 27.4 25 (0.74) (0.97) Year 4 29.9 25 (1.32) (2.11) Standard errors in parentheses.

Curing end bias All told, these studies suggest that end bias gives rise to myopic retrospective voting on

the economy and in other domains. Given the costs of myopia — adverse selection and dead weight loss — I now search for a cure.

As noted above, one explanation for end bias is attribute substitution (Kahneman 2003; Kahneman and Frederick 2002). When engaging in intuitive, low effort judgments, people often substitute a salient attribute for the desired one. Based on self-reports, people think each year should be weighted roughly equally, with slightly more weight given to later years on average (see Table 6). They thus probably desire to base their judgments more or less on total growth during the terms, especially for second term incumbents. Since strong economic performance should lead to more total growth at the end, they may, without realizing it, substitute election-year growth for total growth. If so, presenting plots that more readily reveal total growth should cure them of myopia.

To explore this possibility, I conducted an experiment with two conditions. In the control condition, participants saw yearly growth plots, just like those shown above. In the treatment condition, participants saw both yearly growth and a cumulative growth (one on top of the other). Figure 7 presents an example. The cumulative growth plot simply adds up the current and prior year growth. Although somewhat awkward, the figures nevertheless allow participants to choose between yearly growth and cumulative growth.11 In the instructions for the study, I provided a brief explanation of how cumulative growth relates to yearly growth, an explanation I also included in each cumulative plot.12 The study had 25 terms and used simulated data as described above.

When presented with this choice, do people focus on cumulative growth? That is, do they choose to cure their myopia? To test whether they do, Table 7 shows estimates of the weight given to each years’ income growth when evaluating the four-year economy. The results are

11 In a pilot study, I showed one group just the cumulative plots and the results were the same. However,

participants may not have understood the cumulative plots and may have interpreted them as yearly growth. By showing participants both, they're forced to choose, making misunderstanding less of a concern.

12 After rating all the terms, I tested participants’ understanding of cumulative growth by asking them a simple question that involves calculating cumulative percent from yearly percents. 90% got it right.

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dramatic. When participants saw the standard plot, the end mattered more, as in the studies above. When participants saw both the yearly and cumulative plots, however, they gave roughly equal weight to each year. The difference in weights is most dramatic for the first year: b = .12 in the yearly growth condition versus b = .44 in the cumulative condition.13

A problem with this cure is that cumulative plots are complicated. Another approach to achieving the same goal is, instead of showing people percent change, which seems to trip them up, show levels in the relevant units, such as per capita income in dollars in each year of a term, e.g., $32,500 in the first year, $34,000 in the second, etc. To test whether this would also cure myopia, I picked the previous income growth experiment with the greatest end bias, which was in a gubernatorial study (see Column 4, Table 3). I then tried to cure it by using its randomly drawn income growth data to generate level data. Figure 8 presents an example of a level plot. For the first year of each term, I drew an initial value from a normal distribution with a mean of about $32,000 (the average RDI since 2000) and a standard deviation of 100. The one complication with the level plots is that respondents cannot observe first-year growth, only the first-year level. For them to see first year growth, I would have to show them per capita income from the last year from the previous administration.

As with the cumulative plots, the income-in-levels plots also appear to cure myopia. Column 3 of Table 7 reproduces the original yearly finding of end bias while Column 4 presents the estimates for the level study. Although we cannot compare the first year, the weight participants place on the second year increases substantially, from b = .26 to b = .54, a difference that is highly statistically significant, while the weight they place on last year decreases. In fact, participants in the level study put more weight on the second year than they do on the fourth year (b = .54 versus b = .46). Figure 9 shows this finding visually by plotting average responses against income growth in each year.

In these experiments, participants evaluate multiple terms in short succession. In real-world elections, of course, people only evaluate one term. Do the findings hold when participants only evaluate one term? To see whether they do, I ran a between-subjects version of the levels-in-dollars study with a representative sample of 1602 respondents. I showed the terms in a 20-minute survey that largely focused on other topics. Midway through the survey, participants saw only one of 25 yearly percent growth plots, and recorded their evaluation of the economy for the term. After answering a battery of unrelated questions, participants then saw one of 25 level plots.14 On average, (1602/25 =) 64 participants rated each of the 25 terms. I again told respondents that the plot showed hypothetical, second-term presidents. To analyze the results, I follow the procedures above, taking the average economic evaluation for each plot across all participants who rated it.15 As shown in the last two columns of Table 7 the results do hold when subjects only saw one term. They place more weight on the fourth year when they see the yearly percent growth plot, but do not do so when they saw the level plots. The coefficients are somewhat smaller for both types of plots, indicating a toned down reaction when seeing only one term, but the patterns are the same.

13 These findings are similar to Liersch and McKenzie (2009), who show that end bias vanishes in Varey

and Kahneman’s (1992) original demonstration when pain is presented cumulatively. 14 I chose to show the income-in-levels plots only after showing the yearly-percent-change plots because

the former are unusual, not what people typically see in the news media, and might prompt people to react differently to the yearly-percent change plots. If I had an even larger sample, I would have randomized the order.

15 I also estimated individual-level, within subject models (fixed effects), and found similar results, indicating that the same people waited up the last year in the yearly growth plots but did not do so when, just several minutes later, they evaluated the level plots.

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In the search for a cure, these are important results. If the news media were to convey economic performance with income-in-levels plots, people may not overweight election year.16

Further experiments are needed, but these results are promising. They point to a cure.

Figure 7: Example of cumulative condition

16 Of course, publishing these plots would not solve numerous other problems with retrospective economic

voting, such as the tendency to credit or punish incumbents for economic shocks out of their control.

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Figure 8: Examples of income-in-levels plots Table 7: The cures? Showing individuals cumulative income growth data or showing income in levels appears to cure myopia.

Cumulative growth experiment

Level growth experiment

Between subjects level growth study

(1) (2) (3) (4) (5) (6)

Yearly growth

Cumulative & yearly growth

Yearly growth

Income in levels

Yearly growth

Income in levels

Income growth % Year 1 0.12* 0.44*** 0.11 -0.13 (0.060) (0.063) (0.080) (0.085) Year 2 0.37*** 0.50*** 0.26*** 0.54*** 0.0043 0.12* (0.053) (0.056) (0.073) (0.067) (0.075) (0.060) Year 3 0.46*** 0.54*** 0.40*** 0.37*** 0.18* 0.13* (0.058) (0.061) (0.10) (0.053) (0.087) (0.070) Year 4 0.59*** 0.50*** 0.69*** 0.42*** 0.31*** 0.075 (0.040) (0.042) (0.066) (0.061) (0.079) (0.063) N (terms) 25 25 25 25 25 25 R-squared 0.937 0.936 0.889 0.923 0.496 0.309 SER 0.47 0.49 0.72 0.60 0.82 0.67 N (participants) 54 62 74 47 1602 1602 Note: Standard errors in parentheses. Constant not shown. *** p<0.01, ** p<0.05, * p<0.1

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Figure 9: A cure. Scatter plots for the income in levels experiment. When participants see income levels in dollars (bottom plot), they exhibit less end bias than when they see only yearly percent growth (top plot). The effects are largest for Year 2 (effects for Year 1 can't be estimated)

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Conclusions Retrospective voting assumes citizens are competent evaluators of incumbent politicians'

performance. In this paper, I presented evidence that an end bias generally affects retrospective assessments. When citizens judge incumbent performance on issues such as the economy or crime, their experiences at the end of terms appear to shape their memories of earlier performance.

Using a three-year panel survey, I showed that citizens' memories of the past economy are inconsistent with their actual experience of the economy as they reported it in earlier panel waves. They fail to remember the past correctly in part because the present shapes their perceptions of the past.

I then showed similar behavior in the lab. When participants evaluated economic and crime data, I again found that election-year performance shapes perceptions of overall performance, even under conditions where the election year should not be more informative (second terms).

Finally, I appear to find a cure. Presenting participants with cumulative information on performance (e.g., total income growth) cures myopia. On one hand, these results are troubling for democracy because they confirm citizens’ incompetence at retrospection. On the other hand, they point to a remedy, one that candidates and the news media could adopt.

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Appendix

Four-year vs. four-term experiment To further test whether respondents down weight earlier years because of policy lags, I

conducted another study in which participants evaluated simulated income growth data. I randomly assigned participants to see two versions of the yearly income-growth plots. In the four-year condition, respondents saw plots just like those shown in the yearly-income-growth studies, except I told them that the plots showed yearly income growth in a state for a hypothetical governor’s term, instead of a hypothetical president’s term. In the four-term condition, I told participants that the plots showed the average income growth in each term for governors with especially long tenures: four terms, each of four years. I left the plots exactly the same except I retitled them and relabeled the four income growth bars, not as years 1-4, but as terms 1-4. The figure below presents examples. If a basic cognitive bias gives rise to myopia, I expect them to weight up later terms as much as they up wait up later years. Of course, up weighting later terms could be reasonable, assuming very long policy lags, but up weighting them to the same extent that they up weight later years in a four-year term seems unreasonable.

As expected, participants behave equally myopically when evaluating four-terms as they do when evaluating one term. The table on the next page presents this result, showing regression results using the same setup as for the studies above. The first column shows the results for the four-year condition (which I have already shown in Column 4, Table 3). With years, participants place the most weight on the fourth year (b = .69) in the least weight on the first year (b = .11). With terms, the results are essentially the same, with participants placing the most weight on the last year (b = .69) and the least weight on the first year (b = .18). After respondents evaluated these economies, I again asked them what weights they used. The results are identical to those presented above for both conditions (increasing from about 20% for the first year to 29% for the fourth). In short, this experiment provides yet further evidence that myopia reflects a cognitive bias, not a deliberate strategy.

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Figure 10: Examples of plots from the four-year vs. four-term experiment Table 8: Four-year vs. four-term experiment (1) (2) Four years Four terms Income growth % Income growth % Year 1 0.11 Term 1 0.18** (0.080) (0.070) Year 2 0.26*** Term 2 0.33*** (0.073) (0.070) Year 3 0.40*** Term 3 0.47*** (0.10) (0.10) Year 4 0.69*** Term 4 0.64*** (0.066) (0.067) N (terms) 25 25 R-squared 0.889 0.894 SER 0.072 0.071 N (participants) 74 65 Note: Standard errors in parentheses. Constant not shown. *** p<0.01, ** p<0.05, * p<0.1

Four-year condition Four-term condition

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Average-in-plot vs. no-average experiment I also attempted to cure myopia by including the average growth in the plots (see the example below). As shown in the table on the next page, this slightly reduces end bias.

Figure 11: Example average-in-plot condition

Table 9: Average-in-plot vs. no-average experiment

(1) (2) No average Average Income growth % Year 1 0.15*** 0.31*** (0.047) (0.044) Year 2 0.30*** 0.34*** (0.055) (0.052) Year 3 0.26*** 0.36*** (0.042) (0.041) Year 4 0.67*** 0.60*** (0.065) (0.050) N (terms) 25 25 R-squared 0.909 0.949 SER 0.55 0.45 N (participants) 55 53 Note: Standard errors in parentheses. Constant not shown. *** p<0.01, ** p<0.05, * p<0.1

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