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UBC Theses and Dissertations

Campaign learning and the economy Matthews, John Scott 2006

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C A M P A I G N L E A R N I N G A N D THE E C O N O M Y by JOHN SCOTT MATTHEWS B.A. , Simon Fraser University, 1999 M.A. , Simon Fraser University, 2002 A THESIS SUBMITTED IN PARTIAL F U L F I L L M E N T OF THE REQUIREMENTS FOR THE DEGREE OF DOCTOR OF PHILOSOPHY in THE F A C U L T Y OF G R A D U A T E STUDIES (Political Science) THE UNIVERSITY OF BRITISH C O L U M B I A July 2006 © John Scott Matthews, 2006 11 ABSTRACT The conventional wisdom is that election campaigns facilitate political learning. According to this so-called 'enlightenment thesis,' the contestation and noise of the campaign supplies voters with both the psychological motivation and informational resources to make better vote choices. In this way, election campaigns can be seen as helping overcome one of the central problems of modern democratic politics: chronically low levels of political knowledge across electorates and profound inequalities of political knowledge within them. This dissertation investigates the enlightenment thesis through analysis of the impact of election campaigns on learning in the domain of the economy. In particular, the dissertation examines campaign period change in, first, the quality of national economic perceptions, and second, the quality of the link between national economic perceptions and vote choice. The analysis proceeds through statistical analysis of survey data collected during ten national election campaigns across four countries (Canada, New Zealand, the United Kingdom, and the United States). The dissertation concludes that there is little evidence of campaign period learning in the domain of the economy. There is no general tendency for the campaign to improve the quality of national economic perceptions or to improve the quality of the link between these perceptions and the vote. Indeed, the campaign is as likely to frustrate as facilitate political learning in the economic domain. Furthermore, there is no general tendency for the campaign to offset pre-existing inequalities either in the quality of national economic perceptions or in the quality of the link between these perceptions and vote choice. Apart from its implications for the enlightenment thesis, the dissertation has important implications for broader theories of political cognition. In particular, the analysis calls into question both the theory of information shortcuts and dominant assumptions concerning the impact of cognitive heterogeneity on campaign effects. The dissertation also presents important findings relevant to the study of item non-response, the link between personal and national economic perceptions, partisan bias in political cognition, and economic voting. IV TABLE OF CONTENTS Abstract i i Table of Contents '. iv List of Tables vii List of Figures viii Acknowledgements ix Dedication x CHAPTER ONE Introduction 1 The Enlightenment Thesis 5 Campaign Learning and the Economy 8 Theoretical Complications 9 Critical Assumptions and Analytical Approach 10 Major Findings 13 Little Enlightenment, No Equalization 13 The Psychology of Shortcuts 14 Raw Data and Frames 16 Cognitive Heterogeneity and Campaign Effects 18 Organization 19 CHAPTER TWO The Dynamics of Non-Response in National Economic Perceptions and the Campaign 20 Theoretical Context 21 Item Non-Response 22 The Campaign and Voter Attention 24 Empirical Implications 26 Methodology 27 Measuring National Economic Perceptions 28 Measuring Non-Response in National Economic Perceptions 30 Results 31 The Statics of Non-Response 31 The Dynamics of Non-Response 33 Non-Response Models: General Estimates 34 Non-Response Models: Conditional Estimates 34 Conclusion 36 V CHAPTER THREE The Dynamics of Personal Bias in National Economic Perceptions 44 Theoretical Context : 46 Personal Bias 46 Campaign Economic Discourse 47 The Campaign and Voter Attention 49 Empirical Implications 49 Measuring Personal Economic Perceptions 53 Personal Economic Perceptions and the Campaign 54 Personal Bias in National Economic Perceptions I 57 Personal Bias in National Economic Perceptions II 60 Unemployment Models: General Estimates 62 Unemployment Models: Conditional Estimates 63 Unemployment Models: Interpreting the Dynamics 65 Income Models: General Estimates 69 Income Models: Conditional Estimates 70 Income Models: Interpreting the Dynamics 71 Conclusion 74 CHAPTER FOUR The Dynamics of Partisan Bias in National Economic Perceptions : • 88 Theoretical Context 90 Partisan Bias 91 Campaign Economic Discourse 94 The Campaign and Voter Attention 95 Empirical Implications 95 Methodology 100 Results 102 General Estimates 102 Conditional Estimates 103 Interpreting the Dynamics 105 Conclusion 110 CHAPTER FIVE The Campaign Dynamics of Economic Voting 117 Theoretical Context 119 Economic Voting 119 Campaign Economic Discourse 121 The Campaign and Voter Attention 123 Empirical Implications 123 Methodology 127 Results 129 General Estimates 130 Conditional Estimates 131 vi Interpreting the Dynamics 133 Conclusion 138 CHAPTER SIX Conclusion 145 Limits 147 Technical Objections 147 Constraints on Generalizability 151 Extensions 153 Bibliography 157 Appendix I Data, Question Wordings, and Modeling Details 166 Appendix II Model Results 175 Appendix III Measuring Political Sophistication 254 LIST OF TABLES 2.1. Non-Response in National Economic Perceptions by Sophistication Level by Election 39 2.2. NEP Non-Response and the Campaign: General Model 40 2.3. NEP Non-Response and the Campaign: Estimates by Sophistication Level 41 3.1. Predicted Campaign Effects by Theoretical Assumptions 77 3.2. PEP by Election 78 3.3. PEP Effects on NEP and the Campaign: General Estimates 79 3.4. PEP Effects on NEP and the Campaign: Estimates by Sophistication Level 80 3.5. Unemployment Effects on NEP and the Campaign: General Estimates 81 3.6. Unemployment Effects on NEP and the Campaign: Estimates by Sophistication Level 82 3.7. Income Effects on NEP and the Campaign: General Estimates 83 3.8. Income Effects on NEP and the Campaign: Estimates by Sophistication Level 84 4.1. Predicted Campaign Effects by Theoretical Assumptions 113 4.2. INCPID Effects on NEP and the Campaign: General Estimates 114 4.3. INCPID Effects on NEP and the Campaign: Estimates by Sophistication Level. . 115 5.1. Predicted Campaign Effects by Theoretical Assumptions 141 5.2. NEP Effects on the Vote and the Campaign: General Estimates 142 5.3. NEP Effects on the Vote and the Campaign: Estimates by Sophistication Level . 143 vm LIST O F FIGURES 2.1. The Dynamics of Non-Response (DK) in National Economic Perceptions by Election 42 2.2. The Dynamics of Non-Response (DK + Middle) in National Economic Perceptions by Election 43 3.1. The Dynamics of Personal and National Economic Perceptions by Election .... 85 3.2. Dynamics of Unemployment Effects in NEP by Sophistication Level by Election 86 3.3. Dynamics of Income Effects in NEP by Sophistication Level by Election 87 4.1. Dynamics of Partisan Bias in NEP by Sophistication Level by Election 116 5.1. The Dynamics of NEP Effects on the Vote by Sophistication Level by Election . 144 ix A C K N O W L E D G E M E N T S This dissertation could not have been written without the advice, support and encouragement of numerous teachers, colleagues, friends and family members. First, I would like to thank the members of my dissertation committee, Dick Johnston, Fred Cutler and Paul Quirk, for useful and insightful comments, criticism and direction throughout the research and writing process. In particular, I would like to acknowledge Dick's constant support and mentorship, which began even before my arrival at U B C and will undoubtedly continue for the duration of my academic career. I would also like to acknowledge the encouragement and support of faculty and colleagues at U B C and elsewhere who have influenced, both directly and indirectly, my dissertation research and intellectual development, in particular: Amanda Bittner, Max Cameron, Ken Carty, Rita Dhamoon, Ian Dyck, Lynda Erickson, Peter Ferguson, Alan Jacobs, Karen Lochead, Fiona Macdonald, Mark Manger, Mark Pickup, Paul Warwick, and Russell Williams. Numerous friends have also contributed to this dissertation, some by enduring half-baked oratory on research in progress, others by providing much needed diversion at crucial moments. They are: Mike Bruce, Chad Ellison, Anthony Maragna, James Papadopoulos, Fiona Robinson, and Helen Stortini. James, in particular, deserves special acknowledgement for his (almost) unceasing willingness to explore the intellectual depths, political-scientific and otherwise. Finally, I would like to thank my family for their steadfast support throughout the first decade of my continuing academic adventure. In particular, I would like to thank Eva Matthews, my mother, for her unwavering confidence and limitless patience. X D E D I C A T I O N For Mom. 1 CHAPTER ONE: INTRODUCTION Phillip Converse once observed that political knowledge is a variable with a low mean and a high variance (Converse 1990). By this, Converse meant that the general level of knowledge about public policy and political affairs is low, but that some groups in society—the educated, the politically attentive, and so forth—clearly possess more knowledge than others. The conclusion has been widely reproduced and applies equally well to a range of closely associated variables, including political sophistication, political attention, and political interest (see, inter alia, Campbell et al. 1960; Converse 1964; Butler and Stokes 1971; Sniderman, Brody and Tetlock 1991; Luskin 1991; Zaller 1992; Delli Carpini and Keeter 1996; Fournier 2002). For representative democracy, the implications seem dire. How can democratic institutions properly reflect the preferences of the electorate if most voters lack the ability and motivation to form—or, at least, to express and act on—meaningful preferences over political alternatives? Representative institutions themselves might help. Lupia and McCubbins (1998), for instance, suggest that a suite of political institutions endemic to liberal democracy— such as legislatures and party competition—endow voters with sufficient resources to make reasonable political choices with only a modest amount of political information. Furthermore, the simple process of aggregating the 'error-contaminated' preferences of unevenly informed voters, in the context of elections or public opinion surveys, may also offset the effects of low quantity, low quality political knowledge (Page and Shapiro 1992). But one institution in particular may be of special importance: the informational 2 onslaught of the modern election campaign. The intuition here is that the contestation and noise of the campaign supplies voters with both the motivation and resources to make better informed vote choices (see, for example, Gelman and King 1993; Bartels 1992, 2006; Finkel 1993; Markus 1988, 1992; Anderson, Tilley and Heath 2005; Arceneaux 2005). The dissemination of party platforms, the extensive political reportage in the mass media, the torrent of political advertisements, the direct mobilization efforts of the parties, the conflict and information exchange of candidates debates, the emotional excitement of the race itself—collectively, these are held to fire voter interest in politics whilst simultaneously providing voters with informational resources far greater than those available outside the campaign period. Put simply, on this view, the campaign increases both the supply of and the demand for political information. In this way, it is argued, the campaign might be said to facilitate the "enlightenment" of the voter (Gelman and King 1993). On its face, this 'campaign learning' argument seems persuasive. The claim fits common sense (and some political-scientific) thinking about political cognition and, no less importantly, it also squares with our normative hopes—for an electorate that possesses 'real attitudes' on political matters and that can discipline governments that fail to meet performance expectations. Yet, deeper reflection on what has been termed the "enlightenment hypothesis" (Arceneaux 2005) uncovers reason for considerable doubt. In short, the hypothesis is problematic both theoretically and empirically. The aim of the present dissertation is to contribute to a theoretically sophisticated account of learning during election campaigns. The analysis is unapologetically motivated by the enlightenment perspective on campaign learning, especially as 3 developed in Gelman and King (1993). The enlightenment thesis arguably constitutes the conventional wisdom about political learning in election campaigns (see, for instance, Johnston, Hagen and Jamieson 2004) and, furthermore, represents one plausible pole in theoretical debate concerning the campaign's impact. Yet, the project is equally sensitive to broader work on the roots of political attitudes, perceptions and behaviour. Indeed, this very sensitivity is among the dissertation's important contributions, for attention to the implications of the wider literature underlines the dubious nature of much in the conventional view. A key contribution in this regard is the dissertation's emphasis on the impact of cognitive heterogeneity on campaign learning. Gelman and King (1993) regard campaign learning as a relatively homogeneous process, affecting all voters in roughly equal amounts, notwithstanding pre-existing differences in political knowledge and sophistication. The assumption elides much in contemporary work on political cognition, especially as regards the effects of political communications (e.g. Sniderman, Brody and Tetlock 1991; Zaller 1992; Johnston et al. 1996; Alvarez 1997; Gerber and Green 1999; Lau and Redlawsk 2001). As regards campaign effects, the crucial point is that campaign events and campaign discourse may have different effects on different voters (Ansolebehere and Iyengar 1995; Kahn and Kenney 1997; Johnston, Hagen and Jamieson 2004). A robust form of campaign enlightenment, then, might have asymmetrical effects across the electorate, depending on the voter's 'starting point.' For instance, those who are chronically and assiduously attentive to political matters—the 'political junkies'— will have less to learn than those who awaken to politics only as Election Day approaches. Accordingly, the bulk of the campaign's impact might productively be 4 concentrated among the politically less sophisticated (cf. Mendelsohn and Cutler 2000). In this way, to borrow from Converse, the campaign would not only raise the mean of political knowledge, it would also lower its variance. The analysis is, thus, structured by two central research questions: Do election campaigns facilitate political learning—that is, does the campaign enlighten the voter? And, do election campaigns equalize levels of political sophistication across the electorate? The dissertation's empirical claims rest on statistical analysis of survey data collected during ten national elections across four countries: the five Canadian general elections from 1988 to 2004, the New Zealand elections of 1996, 1999 and 2002, the British general election of 2001, and the US Presidential election of 2000. These data are uniquely suited to analysis of campaign dynamics in voter cognition, having been collected as rolling cross-section (RCS) surveys. RCS survey methodology essentially produces a random sample of respondents for each day of the survey period (typically the length of the campaign), permitting analysis of subtle dynamics in voter cognition as the campaign unfolds (Johnston and Brady 2002). Deploying these data thus affords a uniquely direct examination of the campaign dynamics of political learning. One restriction on the analysis concerns its empirical reach: the dissertation focuses strictly on political cognition in the economic domain. That is, the analysis is confined to, first, the nature and sources of perceptions of the national economy and, second, the nature of links between these perceptions and vote choice. This obviously excludes much that is important to politics. Still, a focus on the economy is a good place to start for several reasons. First, the economy is a ubiquitous political concern— economic matters are central to political contestation and to social well being everywhere. Second, no doubt as a result of this ubiquity, the political psychology of economic perceptions has been widely studied, most prominently in the extensive literature on economic voting. Finally, this thriving research interest in the link between the economy and politics has produced a surfeit of useful data—especially survey data— suitable for addressing questions about a variety of topics, including campaign learning, in a wide range of national and institutional contexts. The remainder of this chapter is organized as follows. First, the enlightenment thesis is treated in some depth, focusing on the central arguments of Gelman and King (1993) and the state of the supporting evidence. Second, the chapter discusses the implications for political cognition in the domain of the economy of both the enlightenment claim (the enlightenment hypothesis) and the notion that the campaign equalizes levels of political sophistication across the electorate (the equalization hypothesis). This section also introduces the dissertation's broad methodological approach. Next, the chapter briefly previews some of the dissertation's major findings, both empirical and theoretical. Finally, the organization of the chapters is discussed. THE ENLIGHTENMENT THESIS Gelman and King (1993) are not so much motivated by the problem of political learning—or "citizen competence" (Kuklinski and Quirk 2001)—as they are by an apparent paradox in the literature on US presidential elections. The paradox is this: election year polls are highly variable, while election outcomes are highly predictable. More precisely, aggregate vote intentions move around quite erratically in the weeks and months before election day, yet the final outcome can be reliably forecasted on the basis 6 of variables (such as economic conditions and presidential performance evaluations) measured months before voters go to the polls. The puzzle is that the former suggests that the ultimate outcome may be the result of a random or quasi-random process, whereas the latter suggests that the outcome is highly structured and turns on 'rational' and easily observable forces. The solution to the paradox, according to Gelman and King (1993), is that the progress of the election campaign informs voters about and focuses voter attention on these rational and easily observable forces—what they term "the fundamentals." The fundamentals, in this sense, include the policy positions of the candidates, candidates' partisan and ideological affiliations, assessments of past government performance, and the state of the national economy. By Election Day, Gelman and King contend, the voter has learned a great deal about the levels of these variables, along with the appropriate weights to accord them in the voting calculus. On this view, then, what appears to be random movement in vote intention instead reflects the unfolding of a learning process, albeit an uneven one. Gelman and King (1993) themselves supply mostly indirect evidence for the enlightenment claim and, notably, they provide no evidence at all that the campaign increases knowledge about and attention to the national economy. Their principal exhibits concern the increasing impact of ideology and race on vote choice over the 1988 presidential election campaign—by their rendering, the impact of both variables grew by roughly 50% in that year. The only direct evidence bearing on the enlightenment hypothesis is in Bartels (2006), and that evidence is mixed. Pooling survey data from two decades of US presidential elections, Bartels finds that the impact of party 7 identification, issue attitudes, candidate evaluations and economic perceptions increases with the approach of Election Day, albeit in varying degrees. The biggest shift is in the impact of issues—effects generally double over the fall campaign. As regards economic perceptions, the effect of the campaign is typically to increase their weight by roughly ninety percent.1 At the same time, however, Bartels uncovers only modest evidence that the campaign moves the fundamentals themselves—that is, that the campaign increases knowledge of key considerations, such as candidate positions and the state of the economy. Significant movement is confined to perceptions of candidates—character and competence judgements, etc.—and, excepting closely fought contests, would have only modest substantive effects on electoral outcomes. These key contributions aside, evidence for the enlightenment claim is largely focused on over-time changes in the impact of—rather than changes in knowledge about—the fundamentals. A spate of work on the US case finds evidence of moderate to strong election year increases in the effects of partisanship, ideology and economic perceptions (Finkel 1993; Campbell 2000; Bafumi, Gelman and Park 2004). Similarly, a handful of cross-national studies depict campaign period increases in the impact of the economy, although the evidence is modest (e.g. Stevenson and Vavreck 2000; Arceneaux 2005; but see Sekhon 2004). Finally, as regards dynamics in knowledge of the fundamentals, a pair of studies—one focused on a Canadian referendum (Mendelsohn and Cutler 2000) and another on a British election (Anderson, Tilley and Heath 2005)— 1 This is the average impact of the campaign on the magnitude of economic effects in presidential vote choice from 1980 to 1996. Bartels drops the 2000 election from the analysis as economic effects actually decline over the course of that campaign, a finding reproduced in Johnston, Hagen and Jamieson (2004) and in this dissertation (see Chapter Five). 8 show increases in a variety of forms of political knowledge over the campaign, in broad agreement with enlightenment expectations. In general, then, evidence of campaign learning is moderately strong, if not entirely compelling. Existing work is undermined, in part, by its typically indirect implications for enlightenment claims, generally weak or inconsistent effects, and, as suggested above, a disproportionate emphasis on dynamics in the weights—rather than the levels—of key variables. Accordingly, the present dissertation aims to present a more systematic treatment of the enlightenment hypothesis. At the same time, as noted above, the analysis extends the enlightenment argument by considering the possibility of equalization in political sophistication across the electorate over the campaign. C A M P A I G N L E A R N I N G A N D T H E E C O N O M Y The enlightenment hypothesis has two major implications for political cognition in the economic domain: 1. The progress of the campaign should improve voter knowledge of economic conditions; and, 2. The progress of the campaign should increase the impact of perceptions of economic conditions on vote choice. The equalization hypothesis has just one pivotal implication: 3. The progress of the campaign should reduce gaps across the electorate in the quality of voter knowledge of economic conditions and in the impact of perceptions of economic conditions on vote choice. These expectations immediately raise complications for empirical research. This section discusses these complications and the dissertation's analytical responses to them. .9 Theoretical Complications The most basic theoretical problem concerns the claim that the campaign 'improves' voter knowledge of economic conditions. Claims about the optimal form and level of knowledge necessary to a sound assessment of the state of the economy are inherently contestable. Leaving aside scientific uncertainty about the way the economy works, what level and form of knowledge the voter requires in order to make a reasonable judgement about the performance of political incumbents is unclear (Kuklinski and Quirk 2001). Furthermore, the very notion of holding governments accountable for economic performance is itself problematic. For example, the impact of the US president on the state of the US economy is, at best, highly mediated (Kuklinski and Quirk 2000). If government action has only minimal effects on economic performance, it makes little sense for voters to hold elected office-holders to account for economic conditions. Still, the dominant political science assumption is that it is sensible for voters to punish and reward governments for changes in the state of the economy (see, inter alia, Key 1968; Kramer 1971; Fiorina 1981; Lewis-Beck and Stegmaier 2000). More precisely, voters with favourable perceptions of economic conditions should support the incumbent, while those with unfavourable perceptions of economic conditions should support the opposition. But what economic perceptions matter? Previous research has focused mainly on two kinds of economic perceptions: perceptions of national economic conditions and perceptions of personal economic conditions. As regards impact on vote choice, the literature is nearly unanimous: it is national economic perceptions that count (see, e.g. Kiewiet 1983; Lewis-Beck 1988; Sears et al. 1993; Mutz 1998; Lewis-Beck and Stegmaier 2000; but see Gomez and 10 Wilson 2003). Even so, what is true empirically need not be true normatively. Certainly the earliest theoretical work on economic voting suggests that it is personal economic well being that should matter (Downs 1957; Key 1968; Kramer 1971). For students of campaign learning, this normative ambiguity presents obvious empirical complications. Even if what is involved in forming sound assessments of economic conditions were obvious, it is not obvious whether national or personal economic conditions—or economic conditions defined by some other unit—are most relevant to vote choice. Critical Assumptions and Analytical Approach In response to these complications, the dissertation applies an analytical strategy that makes few assumptions about what 'proper' economic perception entails. One critical assumption is that it is perceptions of national economic conditions that matter. That is, as noted above, the focus is on voters' evaluations of the state of the national economy and the link between these evaluations and vote choice. This analytical choice seems sensible for two reasons. First, whatever (great or small) impact the national government has on national economic conditions, it is surely more sensible to hold the government responsible for general trends in the whole economy than for particular changes in the lives of individuals, which incorporate both the general trend and random perturbations peculiar to each individual (per Kramer 1971). Second, as noted above, it is national economic perceptions that typically matter to vote choice. Thus, whatever other economic considerations might plausibly and properly be involved in political evaluation, the question of the quality of national economic perceptions and the link between these perceptions and vote choice is crucial. The only other important assumption in the analysis is that, whatever the 'correct' 11 perception of national economic conditions, everyone should share it. That is, no particular, substantive benchmark of economic perception (change in unemployment or gross domestic product, for instance) is assumed. What is assumed, however, is that there is a single valid perception of economic conditions and that, consequently, a fully informed electorate would be unanimous in its economic judgements. This might seem a heroic standard, yet any substantive standard of economic perception must assume at least this much. Furthermore, in principle, meeting this standard only requires that some (more or less) consensual opinion on economic performance is formed at an elite level and that this opinion is then mediated, through whatever means, to the mass. On the dominant view of the relationship between elite discourse and mass opinion (e.g. Zaller 1992), this hardly seems an implausible test of political learning. What, then, does this standard of perceptual quality imply for the enlightenment thesis? Two relevant expectations are examined in this dissertation: First, the progress of the campaign reduces non-response in national economic perceptions; and, second, the progress of the campaign reduces variance in national economic perceptions. The significance of the first expectation should be obvious. The expectation is simply that those who are unable to form or express perceptions of the national economy at the beginning of the campaign are more likely to be able to do so by Election Day. Operationally, the dissertation approaches this question, in Chapter Two, by examining rates of non-response on national economic perceptions queries across the ten campaigns in the analysis. The empirical implications of the second expectation—that the campaign reduces variance in national economic perceptions—are more subtle. On the one hand, the 12 expectation simply implies a negative relationship between the variance of national economic perceptions and campaign time. On the other hand, the expectation could be interpreted more substantively to imply that systematic differences in national economic perception according to social, economic or political characteristics should decline with campaign time. This latter interpretation is critical, for, as discussed below and shown in Chapters Three and Four, national economic perceptions are powerfully conditioned by a range of demographic and political-psychological variables. Insofar as variance in national economic perceptions involves forces other than these known correlates, declining variance in national economic perceptions could co-exist with static or even increasing perceptual bias of political consequence. Accordingly, the dissertation approaches this question by examining dynamics in the magnitude of personal and partisan effects in economic judgement. Specifically, the analysis considers over-time change in, first, the impact of subjective economic perceptions, unemployment, and income (that is, 'personal bias' [Chapter Three]) and, second, the impact of incumbent partisanship (that is, 'partisan bias' [Chapter Four]). In contrast to its implications for economic perception, the implications of the enlightenment perspective for the link between economic perception and vote choice are quite straightforward. Put simply, the expectation is that the relationship between national economic perceptions and vote choice strengthens as Election Day approaches. The dissertation approaches this question, in Chapter Five, by examining dynamics in the impact of economic judgement on incumbent vote intention across the ten elections. This approach parallels existing work (e.g. Gelman and King 1993; Bartels 2006). Similarly, the implications of the equalization hypothesis are fairly obvious. The 13 expectation is that rates of non-response in national economic perceptions, magnitudes of personal and partisan biases in those perceptions, and the impact of these perceptions on vote choice will equalize with the progress of the campaign. An assessment of this hypothesis figures in all of the empirical chapters—from Chapter Two to Five. M A J O R F I N D I N G S The major findings of the dissertation fall into two broad categories. The first category consists of findings directly relevant to the enlightenment and equalization hypotheses. The second category consists of findings and conclusions of broader theoretical import. Each of these findings is now discussed in turn. Little Enlightenment, No Equalization The single most important finding in the dissertation is the profound scarcity of evidence supporting either the enlightenment or equalization hypotheses. First, there is essentially no evidence that the campaign drives down non-response rates on measures of national economic perception. Importantly, non-response rates are generally quite low across the elections examined here. But, what variation as exists is typically cross-sectional rather than time-series: non-response varies with the survey instrument and with levels of political sophistication, but remains static over the campaign. And there is no hint that the campaign equalizes rates of non-response across sophistication levels—whether one considers the information rich or the information poor, the over-time trend is basically flat. Second, there is no indication of a general tendency across the ten elections for the campaign to reduce bias—either personal or partisan—in national economic perceptions. In both cases, the modal effect of the campaign is essentially neutral. That 14 is, the campaign does not reduce bias or erode gaps across sophistication-levels in the magnitude of that bias. And, in the rare case when the campaign does have an effect, it is as likely to accentuate as offset personal and partisan effects on economic judgement, irrespective of sophistication level. In short, the average impact of the campaign on the quality of national economic perceptions is nil. However, there is one, albeit weak, suggestion in the data that the campaign can have 'enlightening' effects. Economic effects on vote choice do regularly—though hardly universally—grow over the ten campaigns examined here. The finding fits neatly with the existing literature, which, as discussed above, regularly—if inconsistently— uncovers evidence that the weight of fundamental variables increases with the approach of Election Day. It seems sensible, then, that the expected pattern turns up only in a minority of the elections examined here. As regards the equalization hypothesis, the results are similarly hopeful, if a little less so: in no case does the campaign increase gaps in the magnitude of economic effects across sophistication levels, and in three cases the campaign shrinks them. Still, overall, the results are significantly at odds with the enlightenment and equalization hypotheses. There is precious little evidence of campaign learning. Even so, these are 'non-findings' that help to identify important theoretical ambiguities and challenges. The Psychology of Shortcuts The expected impact of the campaign on bias in national economic perceptions, and on the link between these perceptions and vote choice, depends crucially on assumptions about the psychology of these connections. If the campaign is to erode bias 15 in economic judgement, for instance, personal and partisan effects in national economic perceptions must function as information shortcuts. A shortcut, in this sense, can be defined as an inference process that permits the formation of sound attitudes and perceptions concerning a given object in the absence of information directly relevant to that object. The general idea originates with Downs (1957) and has lately become central to much work in political psychology (see, especially, Sniderman, Brody and Tetlock 1991; Popkin 1991; Lupia and McCubbins 1998; Lupia, McCubbins and Popkin 2001). For campaign learning and knowledge of the economy, the pivotal implication of the shortcuts argument is that as information directly relevant to economic perception is acquired, reliance on information shortcuts should decline. If the campaign supplies useful economic information, then, personal and partisan biases in economic perception should shrink as Election Day approaches. A key implication of the results in the dissertation is that such shortcuts claims are facile at best—at least as regards information processing in election campaigns. For one thing, as noted above, there is little evidence that the campaign erodes bias in economic perception in the theoretically expected manner. For another, even if personal and partisan biases do reflect the operation of information shortcuts, it is far from clear that the progress of the campaign should offset them. A central theoretical distinction developed in subsequent chapters is between images of shortcuts as automatic and non-automatic. An automatic shortcut is one that an individual can use in the absence of significant direction or cueing from the environment. A non-automatic shortcut, by contrast, is one that requires a non-trivial amount of such cueing. Crucially, if a shortcut is non-automatic, the acquisition of information during an election campaign may, in fact, 16 increase shortcutting, providing that campaign discourse contains the relevant cues (on this point, more below). As discussion in subsequent chapters demonstrates, the dissertation can arrive at only tentative conclusions regarding such theoretical questions. Yet it seems clear that personal and partisan effects in economic judgement, on the one hand, and economic effects in vote choice, on the other, do not reflect the operation of automatic shortcuts. They may indicate non-automatic shortcutting or even such non-conscious processes as selective attention and perception. The discriminating factor here may be assumptions about the nature of campaign discourse. Raw Data and Frames Whatever the psychological basis of personal and partisan effects in economic perception and, indeed, of economic voting itself, the nature of campaign discourse relating to the economy matters a great deal. Later chapters introduce an important distinction between two kinds of discourse: raw economic information, or simply raw data, and framing discourse. Raw data is information that is directly relevant to the formation of attitudes and perceptions concerning a given object. As regards national economic perceptions, for instance, raw data might include explicit reports concerning key economic indicators, such as change in the Gross Domestic Product or in unemployment levels, and also more summary interpretations of the state of the economy, such as television news reports of general changes in economic conditions. As regards vote choice, raw data would include detailed information on the administrative competence and policy positions of incumbents and challengers. The important point in both cases is that this sort of 17 discourse is the kind of directly relevant information for which, in its absence, individuals might substitute an information shortcut—such as falling back on personal economic experience to make an inference about the performance of the national economy.2 Framing discourse, in this context, is discourse that posits connections between attitudes and perceptions. As regards national economic perceptions, this kind of discourse might take the form of explicit attributions of credit and blame for economic outcomes to parties and candidates, or it may encourage explicit links between personal economic experiences and national economic conditions. Such discourse should facilitate, respectively, partisan and personal biases in economic judgement. As regards vote choice, framing discourse would make clear links between political evaluation and the performance of the economy—as above, this could take the form of attributions of credit and blame or it may appear as more general discourse about the importance of 'economic competence' as a consideration in the vote decision. The key point is that, in both cases, such discourse should facilitate the formation of economic and political attitudes and perceptions in the absence of information bearing directly on these matters—that is, in the absence of raw data. The raw data-framing discourse distinction is important theoretically, for each kind of information makes a different potential contribution to campaign learning. Specifically, raw data should reduce shortcutting, while framing discourse should increase it. One important possibility, consequently, concerns the implications of campaign discourse that is 'mixed'—discourse that combines raw data and framing cues. 2 It bears emphasis that 'raw data,' in this sense, does not mean 'unprocessed data.' That is, raw data does not include only 'raw numbers'—it can equally include more summary interpretations of economic or political trends and conditions. 18 Depending on the relative weight of the two kinds of information, the progress of the campaign may have offsetting effects on political learning. Indeed, the campaign may facilitate the use of shortcuts even as it reduces the need to do so. Thus, a finding of null campaign effects—a recurring motif in the chapters ahead—may conceal a great deal of theoretically interesting psychological action. Cognitive Heterogeneity and Campaign Effects As noted at the outset of this chapter, one of the central contributions of the dissertation is a focus on the significance of cognitive heterogeneity for campaign learning. Existing literature on campaign effects, and on the impact of political communications more generally, emphasizes the potential for the magnitude of effects to vary across levels of political attention, knowledge and sophistication (see, especially, Zaller 1992; Ansolebehere and Iyengar 1995; Johnston et al. 1996; Kahn and Kenney 1997; Alvarez 1997; Gerber and Green 1999; Johnston, Hagen and Jamieson 2004; Fournier et al. 2005). Varying effects of this sort are crucial to the equalization hypothesis: if the information poor are to catch up to the information rich, the former must benefit disproportionately from the campaign learning process. Yet, as noted above, the dissertation uncovers little evidence of these kinds of dynamics—most of the time, the gap between the sophisticated and unsophisticated is undisturbed by the campaign. Even so, much in the analysis to come does underline the importance of cognitive heterogeneity. Indeed, several chapters find evidence of campaign effects that vary not only in magnitude, but also in direction. For instance, in some cases, the campaign increases bias in economic perceptions among the unsophisticated, even as it shrinks the 19 bias among the sophisticated. Or, alternatively, the campaign shrinks economic effects on vote choice among political sophisticates, while priming economic considerations among everyone else. The evidence is scattered and hardly conclusive, but it draws attention to an important theoretical possibility: using shortcuts requires sophistication, but it requires even more sophistication not to use them. This is a perversion of the standard shortcuts claim, but squares with dual process models of information processing in social psychology (e.g. Petty and Cacioppo 1986; Eagly and Chaiken 1993). Thus, the campaign may supply low sophistication voters with just sufficient motivation and appropriate framing discourse to make use of shortcuts, at the same time as it motivates high sophistication voters to pay careful attention to raw data, which may be more cognitively demanding in any case. O R G A N I Z A T I O N The organization of the dissertation is previewed above. Chapter Two examines the dynamics of non-response in national economic perceptions; Chapters Three and Four treat dynamics in personal and partisan biases in national economic perceptions, respectively; and Chapter Five considers dynamics in the impact of national economic perceptions on vote choice. Chapter Six concludes. Methodological details are largely presented in the chapters, including discussion of key variables. Modelling details, exact question wordings, complete model results, and an extended discussion of the construction of the dissertation's measure of political sophistication appear in Appendices I, II and III. 20 CHAPTER TWO: THE DYNAMICS OF NON-RESPONSE IN NATIONAL ECONOMIC PERCEPTIONS AND THE CAMPAIGN Survey respondents report that they 'don't know' the answer to a given question for a variety of reasons. Social norms, for instance, can induce a respondent to edit his/her responses for socially inappropriate content, leading, in some cases, to 'don't knows'—or more technically, to item non-response (Berinsky 1999, 2002, 2004). A simple deficit of motivation to respond to a particular survey also promotes 'don't knows,' as respondents may engage in "satisficing" behaviour that mollifies the interviewer with a minimum of effort (Krosnick 1991). Finally, cognitive factors such as attitudinal ambivalence or the simple difficulty of the task can also lead to item non-response (Tourangeau, Rips and Rasinski 2000; Krosnick 1991; Shoemaker et al. 2002). A campaign that promotes political learning should offset the effects of these processes. In particular, as regards non-response in national economic perceptions (or NEP), an 'enlightening' and 'equalizing' campaign should have two major impacts: First, the progress of the campaign should lead to a decline in the proportion of respondents, irrespective of sophistication level, who say that they 'don't know' the state of national economic conditions. Second, the approach of election day should equalize rates of non-response in national economic perceptions across sophistication levels—that is, the campaign should 'narrow the gap' between the information rich and the information poor. Happily, theory suggests that the campaign should promote political learning of this sort, at least in some degree, under a rather broad set of conditions. In short, the 21 informational output and attractive force of the campaign should help the voter to overcome deficits on both the cognitive and motivational sides of the psychological ledger. Although the possible sources of economic perception are varied—and the precise nature of these sources is contestable, as discussed in subsequent chapters—the campaign should generally supply information to help the voter to form economic judgments, and also the motivation necessary to do so. The results reported in this chapter, however, offer not the slightest hint that the campaign tends to have such an effect. Any impact of the campaign on non-response in national economic perception is mostly undetectable. And, in the rare case when the campaign does have some appreciable impact, it would seem as likely to increase as decrease the share of 'don't knows.' Moreover, there is no indication that the campaign narrows the significant, pre-existing gap across sophistication levels in the likelihood of non-response in national economic perceptions. By this one, rather summary standard then, the impact of the campaign seems neither enlightening nor equalizing; it seems, on the contrary, basically neutral. The chapter proceeds as follows. First, the theoretical background is reviewed. Next comes discussion of methodology. The substance of the analysis is in the third section of the chapter, with detailed treatment of results. The final section concludes. THEORETICAL CONTEXT For expectations about the campaign's impact on non-response in national economic perceptions, two areas of theoretical concern are important: the nature of item non-response and the impact of the campaign on voter attention to political discourse. Fortunately for the campaign learning view, all combinations of plausible assumptions in 22 these domains lead to the expectation that the campaign generally reduces item non-response. Furthermore, half of these combinations of assumptions also lead to the expectation that the campaign narrows the 'non-response gap' in national economic perceptions. Note, however, that the non-uniqueness of the predictions across these various possibilities must inevitably produce a certain theoretical indeterminacy in the analysis; this point returns below. But first, this section reviews the theoretical terrain. Item Non-Response The major roots of item non-response fall into two broad categories: motivational and cognitive. With respect to the former, Krosnick (1991) argues that the most important factor is the tendency of survey respondents to "satisfice." Satisficing behaviour occurs when a respondent settles on and expresses the first acceptable answer—one that will satisfy the interviewer—rather than the answer that reflects the respondent's 'true attitude,' or, at least, the attitude the respondent would express given more intensive cognition about the survey question and the various considerations it raises. Satisficing behaviour can include random responding, a failure to differentiate among diverse objects of evaluation,1 and, crucially, item non-response. For the present chapter, the important point about satisficing is that the tendency to satisfice is negatively related to the respondent's motivation to respond to a given survey. And in this regard, the impact of the campaign may be decisive; that is, the campaign should increase respondents' motivation to answer survey questions concerning political matters. Gelman and King (1993) certainly assume that the 1 A failure to differentiate among diverse objects of evaluation may have occurred when, for example, a respondent asked to rate a number of candidates expresses the same attitude (e.g. a rating of 50 on a feeling thermometer) toward each candidate. 23 approach of Election Day increases the motivation to attend to political matters. In a more general vein, Krosnick (1991) suggests that respondent motivation for survey participation should increase insofar as participation is viewed as "important and/or useful to some segment of society" or is viewed as personally important (224). It seems plausible that the civic exhortations and emotional excitement of the campaign make political participation of all kinds—including participation in opinion surveys—seem more important socially and personally, at least relative to the non-campaign period. Thus, the typical campaign should drive down rates of non-response on political survey items, including questions regarding national economic perceptions. As regards cognitive sources of item non-response, the major factors are the difficulty of the cognitive task required by a given survey question and the respondent's ability to execute that task (Krosnick 1991; Shoemaker et al. 2002; Berinsky 2004). "Task difficulty," as Krosnick (1991) terms it, can include the nature of the memory retrieval process entailed by a survey question, the number of distinct objects a question addresses, and the nature of the judgement process a question requires. The respondent's ability to execute a given survey task can depend on, among other things, the "amount of practice" the respondent has in thinking about a given topic and on whether or not the respondent already possess a "preconsolidated attitude" relevant to the issue or perception in question (Krosnick 1991; see also Tourangeau, Rips and Rasinski 2000). And, of course, the simple acquisition of information helpful in answering a survey question is also important, whether that information is directly relevant to the attitude concerned or facilitates an inference process, such as shortcutting, that can enable attitude formation (on both these possibilities, see below and Chapters Three, Four and Five). 24 For the question of campaign learning, the important cognitive factor is respondent ability. As suggested above, the campaign should increase voter motivation to attend to political matters and for political participation more generally, including political discussion and political attitude formation. These kinds of behaviours inherently increase the voter's cognitive 'practice' with political matters and should also raise the likelihood that the voter qua survey respondent will already possess a 'preconsolidated attitude' on a variety of politically relevant topics, including the condition of the national economy. Furthermore, the campaign should also, as suggested above, supply information directly and indirectly relevant to economic perception, either in the form of 'economic raw data' or 'framing cues' that may facilitate an inference process (see Chapter One). Thus, the campaign should reduce the likelihood of non-response on queries concerning economic judgments, for both motivational and cognitive reasons. The Campaign and Voter Attention Expectations about the impact of the campaign on voter attention are crucial to evaluating the argument that the campaign offsets pre-existing inequalities in political learning. The key concern is the way in which the campaign's motivational and cognitive impact is articulated across the spectrum of political sophistication. The crucial question is, thus, for whom does the campaign matter, and how? An important prior theoretical concern is the impact of political communications across sophistication levels in general. For the present analysis, two variables are important in this regard. The first is the likelihood of exposure to political communications, especially as indexed by variables such as political interest and 2 Evidence that the campaign increases levels of political knowledge in general lends credence to this view (Mendelsohn and Cutler 2000; Anderson, Tilley and Heath 2005). 25 attention. Increasing levels of sophistication tend to imply increasing interest and attention (Luskin 1987; Zaller 1992, 1996; Price and Zaller 1993; Delli Carpini and Keeter 1996), and so high sophistication individuals should, all other things being equal, be most responsive to campaign discourse. However, all things are not likely to be equal, as sophistication also should be positively correlated with a variable that should limit response to campaign discourse: the weight of previously acquired information. The variable is crucial to Bayesian models of political learning, such as that of Gerber and Green (1999), and also figures in longstanding arguments concerning the stability of partisanship (Converse 1962). The argument, in short, is that the attitudinal impact of new information is constrained by the accumulation of information preceding it. Thus, among the information rich, the positive effect of attentiveness on the impact of campaign discourse may be offset by a comparable negative effect from the weight of previously acquired information. For campaign effects, the summation of these opposing forces may imply roughly equivalent effects across sophistication levels. The progress of the campaign, however, may disrupt this pattern. In particular, the campaign may untie the link between political sophistication and attention. As suggested above, the noise and excitement of the campaign should increase the intrinsic interest of politics and, by extension, voter motivation to attend to political developments. However, the motivational gains may not be spread evenly across the electorate. Indeed, the impact of the campaign may be concentrated where it can do the most 'good'—that is, among the chronically uninformed, uninterested and inattentive. Evidence suggesting that campaign effects maximize among low information voters comports with this view (Ansolabehere and Iyengar 1995; Kahn and Kenney 1997; Johnston, Hagen and Jamieson 26 2004; Arceneaux 2005). In general, three possible assumptions about the impact of the campaign on voter attention seem plausible. First, the campaign has no impact on voter attention. In this case, the campaign should, as suggested above, have roughly equivalent effects across sophistication levels (i.e. among high and low sophistication voters). Second, the campaign increases voter attention in equal amounts across pre-existing levels of political sophistication. In this case, the campaign should, again, have similar effects across sophistication levels. Finally, the campaign increases voter attention primarily among low sophistication voters. The expectation in this case, consequently, would be for campaign effects to maximize among the chronically il l informed.4 Empirical Implications Overall, then, theory leads to quite sanguine expectations about the impact of the campaign on non-response in national economic perceptions. Whether the campaign's effect is primarily motivational, primarily cognitive or some combination of both, the consensus prediction is that the approach of Election Day reduces levels of non-response in queries of economic judgments. And, if the campaign excites interest disproportionately among low sophistication voters, the process should also narrow the 3 The exact distribution of effects depends on assumptions about the relative weight of exposure and ex ante information (i.e. the weight of previously acquired information) in determining the magnitude of the campaign's impact across information levels. In the present analysis, however, indicators of the relevant quantities are too imperfectly measured for subtle predictions of this sort. 4 Note that the opposite expectation—that the campaign increases voter attention primarily among sophisticates—is excluded here, on the assumption that the campaign's impact on voter attention diminishes with ex ante levels of attentiveness. Accordingly, it seems reasonable to expect attention increases among the sophisticated to be constrained to, at most, equality with attention increases among the unsophisticated. This assumption fits evidence of maximum campaign effects among low information voters (Ansolabehere and Iyengar 1995; Kahn and Kenney 1997; Johnston, Hagen and Jamieson 2004; Arceneaux 2005) and also simplifies the analysis. 27 gap in non-response across sophistication levels. In short, there are good theoretical reasons to suspect that the campaign is both enlightening and equalizing as regards non-response in national economic perceptions. M E T H O D O L O G Y The analytical approach is to regress, for each of the ten elections, indicators of non-response in national economic perception on a variable measuring campaign time. Separate estimates of the models are presented for all voters, high sophistication voters and low sophistication voters. Three equations figure in the analysis: NEPDK = f(p0 + $\DAY + u), (2.1) NEPMID = f(p\, + $\DAY+ u), (2.2) NEPDKMID = f(po + $\DAY + u), (2.3) where NEPDK = 'Don't know' response to NEP item; NEPMID = middle response to NEP item; NEPDKMID = 'Don't know' or middle response to NEP item; DAY = day of campaign; and, u = random error. Construction of the indicators of non-response is discussed in some detail below. The measure of campaign time, DAY, is simply the day of the campaign. The variable is a counter that starts at 1 on the first day of the campaign period and reaches its maximum (which varies across elections) on the day before Election Day. The longest campaign in the analysis is the US Presidential election of 2000—for analysis of that election, the counter runs from 1 to 62. The beginning of the general election campaign in the US is typically fixed at the day after Labour Day (Campbell 2000; Johnston, Hagen and Jamieson 2004) and that convention is adopted here. The start of the remaining 28 campaigns is set to the day on which Parliament is dissolved—or 'writ day'—making these campaigns roughly half as long as in the US case.5 A negative coefficient on the DAY term in any of the equations indicates that the progress of the campaign reduces the likelihood of non-response in national economic perceptions. The measurement of political sophistication is somewhat more complex and merits extended discussion; this appears in Appendix III. Note that, where possible, political sophistication is measured with indicators of general, factual political knowledge, following best practices in the literature (Price and Zaller 1993; Delli Carpini and Keeter 1996). Where this is not possible, political sophistication is measured using indicators of general political interest and media attention, both alone and in combination. Irrespective of the measurement details, for each election, the indicator of political sophistication is split at its midpoint to yield high and low sophistication groups. Measuring National Economic Perceptions Economic effects on vote choice have been widely studied, so survey instrumentation concerning economic evaluations is commonplace and reasonably comparable across surveys. In the present sample of elections the typical item is some minor variation on the following: How do you think the general economic situation in New Zealand now compares with a year ago? Is it the same, better or worse? [NZES 1999] A l l but two of the surveys contain an item of this sort.6 In the deviant surveys, the NAES 5 Campaign lengths (days): Canada, 1988: 48; Canada, 1993: 45; Canada, 1997: 36; Canada, 2000: 34: Canada, 2004: 36; New Zealand, 1996: 37; New Zealand, 1999: 30; New Zealand, 2002: 36; United Kingdom, 2001: 30; United States, 2000: 63. 6 A l l economic perceptions items are, of course, from the campaign wave of each survey. Exact question wordings are reproduced in Appendix I. 29 2000 and NZES 2002, the relevant items query respondent attitudes toward the economy "today" and "these days," respectively. Both items have been found instructive in previous analyses of these elections (Johnston, Hagen and Jamieson 2004; Vowles et al. 2004) and are suitable proxies for the more standard retrospective measure.7 The difference is not without consequence, however—this point is taken up later in this chapter. Even so, a more important source of wording variation across the surveys is in the number of response categories offered to respondents. In six surveys, respondents are offered five levels of response (Canada 1988 and 1993, New Zealand 1996 to 2002, Britain 2001). In three surveys, three categories are available (Canada 1997 to 2004). In one survey (US 2000), four categories are presented to respondents. This variation is important insofar as respondents have a tendency to moderate their attitudes by expressing qualified responses (Krosnick 1991; Tourangeau, Rips and Rasinski 2000; see also discussion in Chapter One). The items from the 1988 and 1993 Canadian Election Studies, for instance, permit respondents to moderate their expressed attitudes by adding a "somewhat" qualifier to their assertions that the economy has "gotten better/worse". In the later Canadian studies, by contrast, respondents who wish to do so are denied such an opportunity to waffle. The potential consequences are threefold: (1) insofar as respondents with strong directional (i.e. intense and non-neutral) attitudes moderate their attitudes in the five category surveys, aggregate measures of economic perceptions will be biased toward the middle; (2) insofar as respondents with moderate directional attitudes can not moderate 7 In the post-election wave of the NZES 2002, for instance, there is a relatively strong correlation between the 'current' economic evaluation measure and a more standard retrospective measure: r = 0.49. 30 their attitudes in the three (and, to a lesser extent, four) category surveys, aggregate measures of economic perceptions will be biased away from the middle; and (3) insofar as (1) and (2) are true, variance in economic perceptions will, ceteris paribus, be greater in the three category surveys than in the four and five category ones. Point (3) is most relevant to hypothesis testing, as the higher variance questions produce smaller standard errors than the lower variance questions, making rejection of null hypotheses easier. On the whole, however, the measures of national economic perceptions are highly comparable across the ten election studies. And, in any case, the wording variations are of little consequence to the analysis in the present chapter. Measuring Non-Response in National Economic Perceptions As represented in equations (2.1) to (2.3), non-response in national economic perceptions is measured by three different indicator variables: NEPDK, which indicates a 'Don't know' (DK) response; NEPMID, which indicates a middle response; and NEPDKMID, which indicates a 'Don't know' or middle response. This approach is taken for both practical and theoretical reasons. The practical reason is that for one of the ten elections (United Kingdom 2001) DKs are not reported. The theoretical reason, following Krosnick (1991), is that the middle category may be a 'hiding place' for respondents who, in actuality, 'don't know' what they think about the state of the economy. Pursuant to the 'satisficing' logic described above, some respondents may find it easier to give a non-directional but superficially valid response than to admit that they 'don't know' the answer to a given question. Indeed, the problem may be acute in the present analysis, as none of the surveys prompts for 'don't knows'. Of course, those giving middle responses (in most questions, those who think the economy is 'about the 31 same' as it was a year earlier) are not necessarily 'non-responsive.' It is difficult to separate the two groups cross-sectionally. Looking over time in the campaign, however, erosion in the middle response category may reflect political learning. Still, NEPMID is a poor substitute for NEPDK, so emphasis is placed on the latter. R E S U L T S Analysis proceeds in four parts. First, the static distribution of non-response on national economic perceptions is presented for each election, both across the sample as a whole and within subgroups defined by sophistication level. Next are plots of the over-time distribution of non-response for each election. This is followed by discussion of general estimates of the non-response models; these estimations pool observations across sophistication levels. The final section presents conditional estimates of the models, reporting separate results for high and low sophistication respondents. The Statics of Non-Response Table 2.1 reports the distribution of non-response in national economic perceptions across the ten elections, both within and across sophistication levels. Taking the samples as a whole, the average proportion of DKs across the nine surveys for which 'don't knows' were recorded is quite modest—roughly 3 percent. The highest rate of non-response is for Canada 1988 at 5.42%, the lowest rate is for New Zealand 2002 at 0.48%. Most of the inter-survey variance in non-response would seem to be explained by question wording variation. As noted above, a measure of current economic perceptions is substituted for the standard retrospective measure in two cases: New Zealand 2002 and US 2000. The 'current' measure, which requires only knowledge of present conditions, is intrinsically easier for respondents than the retrospective one, which requires 32 knowledge of both present and past economic conditions. The retrospective measure, moreover, involves a more sophisticated cognitive task—a comparison of two economic conditions at two time points rather than simply the recall of economic conditions at one time point. These two variations in the retrieval and judgemental demands of the two questions are probably sufficient to explain the stark contrast between, for instance, the proportion of DKs in the 1988 CES and the 2002 NZES. Remaining variation across the studies is not readily interpretable. Breaking the samples down by sophistication level, the general pattern fits theoretical expectations perfectly: in every case, the proportion of 'don't knows' among high sophistication voters is smaller than among low sophistication voters. In some cases, the contrast is very striking. In the United States in 2000, for instance, there were more than six times as many DKs among low sophistication respondents as among high sophistication respondents. In Canada 1993, the ratio of low sophistication to high sophistication 'don't knows' was 5 to 1. The results suggest two important conclusions: the broad theoretical approach is on track—i.e. more information means less non-response—and the measures of political sophistication are sensible. Results when using the proportion of middle responses as an indicator of non-response parallel those for NEPDK. The total share of middle responses varies quite widely—from 47.98% in Canada 2004 to 20.80% in New Zealand 2002—likely because this category is populated by both 'true middle responders' and 'non-responders.' As regards rates of non-response across sophistication levels, in seven of the nine elections for which middle responses are recorded, the proportion of middle responses is greater among low sophistication than among high sophistication respondents. A similar pattern 33 Q emerges when DKs and middle responses are combined. This suggests, once again, that the general theoretical intuition is correct and, furthermore, that the middle category may be a plausible surrogate for non-response. The Dynamics of Non-Response Cross-sectional variation in the overall 'don't know' share is, of course, not instructive as regards campaign learning. In this regard, Figures 2.1 and 2.2 are a useful first step. The figures portray the over time dynamics of NEP non-response by plotting, for each election as possible, the daily share of 'don't knows' (Figure 2.1) and the daily sum of the 'don't know' and 'middle' shares (Figure 2.2). To clarify any trends, as may exist, shares are smoothed by LOWESS (bandwidth=0.3).9 What strikes the eye is the general lack of any campaign dynamics in rates of non-response, whether one considers the D K share or combined D K and middle shares. In other words, almost all the lines are essentially flat. One exception is the share of middle responses on the NEP measure for Canada in 2004: perversely, the proportion of respondents saying the national economy was 'about the same' as the year before increased by roughly half over the campaign, with most of the action occurring during the campaign's final ten days. A more indulgent review of the plots might find other dynamics—one might, for instance, see early drops in the D K share in Canada in 1988 and 2000—but the overall picture clearly suggests that the campaign's impact on non-response is essentially nil. In six of the eight elections concerned, the mean of NEPDKMID is higher among low than among high information respondents. 9 LOWESS stands for locally weighted least squares, a form of nonparametric regression (Cleveland 1994). 34 Non-Response Models: General Estimates Eyeballing the over-time plots, of course, is hardly a convincing test for dynamics. Do the conclusions of the graphical analysis stand up when tested statistically? The results in Table 2.2 are more decisive. The table contains logit estimates for Pi from equations (2.1) to (2.3) (complete model estimates reported in Appendix II). The results only confirm the graphical analysis. The most obvious fact about the table is its high population of zeros, whether one examines DKs, middle responses, or the summation of the two. Thus, any (linear) impact the campaign might have on non-response—however measured—must be vanishingly small. And, indeed, all but one of the coefficients is indistinguishable from zero by conventional standards. The one coefficient that does achieve statistical significance—-in the estimate for model (2.1) for Canada 2004—is not 'correctly' signed: as indicated in the graphical analysis, the proportion of 'don't knows' would seem to have increased over that campaign. Statistical significance aside, roughly half the coefficients in the table (11 of 23) are 'incorrectly'—that is, positively—signed. The overall pattern, then, is clearly at odds with theoretical expectations. The campaign's effect seems neutral at best, as likely to increase as decrease rates of non-response at worst. Does the conclusion hold up when conditioning on sophistication level? Non-Response Models: Conditional Estimates Table 2.3 contains estimates of Pi from equations (2.1) to (2.3) by sophistication level (complete model estimates reported in Appendix II). The results agree neatly with 35 the general estimates: most of the coefficient estimates are insignificant by substantive and statistical standards, irrespective of the sophistication level or measure of non-response one considers. Considering results for NEPDK first, just two of eighteen coefficients are statistically significant—one negatively signed (low sophistication respondents in Canada 2004), one positively signed (low sophistication respondents in New Zealand 1996). Two other negatively signed coefficients approach statistical significance (high sophistication respondents in New Zealand 1996 and 2002). Still, no coefficient is substantively large and most are vanishingly small. There is a weak negative tendency among the coefficients—11 of 18 are negative—but the end-of-campaign impact of most of these trends on levels of non-response would be substantively miniscule. Looking across sophistication levels, there is little evidence of a tendency for the campaign's effect to be concentrated among one group of voters: although both significant effects are found among low sophistication voters, this may be mostly a result of the thinly populated ranks of the sophisticated (at least in New Zealand, where effects approaching statistical significance among high sophistication respondents are found). Overall, then, the results diverge wildly from campaign learning expectations, not to mention a host of theoretical arguments. There is only the weakest of evidence that the campaign leads to any decline in rates of non-response on national economic perceptions and no evidence at all that the campaign tends to narrow the gap in non-response across sophistication levels. The picture changes little when considering levels of middle response over the campaign. Campaign effects tend to be smaller for models of NEPMID than for models of NEPDK, and none of these are statistically significant. Worse, 11 of the 16 36 coefficients concerned are positively signed. Likewise, among models of NEPDKMID, only one coefficient is statistically significant (for Canada 2004) and it too is positively signed, along with 10 of its 13 counterparts for other elections. The general picture, thus, is in striking contrast to the conventional wisdom. The campaign's typical impact on non-response in national economic perceptions is, in a word, nil. C O N C L U S I O N Theory strongly implies that non-response in measures of national economic perception should drop with the approach of Election Day. The reasons are twofold. First, the campaign should supply survey respondents with information sufficient to surmount at least some of the cognitive barriers to attitude formation. Second, even if the campaign fails to inform, it should motivate: the progress of the campaign should excite sufficient interest in politics to induce respondents to make better use of whatever informational resources are at hand. In view of this, the results in the present chapter are quite surprising. In short, the analysis suggests that the typical impact of the campaign on non-response in economic judgement is insignificant, both substantively and statistically. Almost all estimated effects are indistinguishable from zero. This is so whether one considers all respondents together or stratifies by political sophistication. Those effects that do clear standard significance thresholds—or even just approach them—are nevertheless small and, in any case, as likely to be positive as negative. That is, the campaign is as likely to increase as decrease non-response in national economic perceptions. The most important fact, however, is that the likelihood of the campaign having any effect is very small. 37 For campaign learning, the implications are troubling. There is no tendency, by this standard, for the campaign either to enlighten or equalize—non-response does not drop and gaps in non-response across sophistication levels are not narrowed. And the results are equally troubling for theory. As noted above, the expectation that the campaign should drive down rates of non-response in economic perception is a consensus prediction—any way you slice it, the campaign should have such an effect. Where, then, does theory go wrong? It seems implausible that increases in information and motivation do not reduce item non-response. The empirical literature in this regard is compelling (see, e.g., Krosnick 1991; Berinsky 1999, 2002, 2004; Tourangeau, Rips and Rasinski 2000; Shoemaker et al. 2002) and the general finding is neatly reproduced in the present chapter (rates of non-response are clearly graduated by sophistication level; see Table 2.1). More plausible is the possibility that standard assumptions about the nature of the campaign's motivational and informational impact are incorrect. First, the campaign may not motivate, at least, not in general and not to a very great extent. One's appetite for politics might be fixed in childhood—or perhaps in young adulthood—and largely impervious to later influences (cf. Luskin 1991). If this is so, one's level of excitement (or diffidence) for participation in political surveys should be unchanged by the approach of Election Day. Alternatively, the campaign may generate interest mainly among those who are already interested—and who are, consequently, already able to form and express valid perceptions of economic conditions. And this makes a certain sense: the likelihood of exposure to the campaign stimulus is a function of prior motivation, so the unique inducements of the campaign period should 38 redound to the already motivated. Either way, the expectation for non-response over the campaign would be stasis. Another possibility is that the campaign may not inform; that is, the campaign may not supply survey respondents with information that, on balance, is helpful in the formation of economic perceptions. As discussed in Chapters Three and Four, there are multiple routes to the formation of economic perceptions: personal economic experiences, partisan commitments, economic information supplied by the media, and the state of the economy itself. Insofar as these different sources of economic judgement point in different directions, the survey respondent may find him/herself in a state of ambivalence. Imagine, for instance, an incumbent partisan who has recently experienced job loss. The dissonant implications of this situation may lead to political withdrawal, from both the survey interview and the voting booth. A l l is speculation. But the speculations are bolstered by the striking homogeneity of the empirical pattern. In any case, it seems clear that theory about the impact of the campaign on item non-response, especially in the economic domain, is in need of serious revision. The campaign's effect may be more complex—and more elusive—than has lately been imagined. Table 2.1. Non-Response in National Economic Perceptions by Sophistication Level by Election Information D K + Level D K Middle Middle Information Level D K D K + Middle Middle Canada 1988 Total 5.42 47.85 53.27 New Zealand 1996 Total 2.85 37.42 40.28 High 3.98 44.11 48.09 Low 7.01 51.78 58.80 High Low 2.78 2.84 34.90 37.96 37.69 40.80 1993 Total 1.85 28.26 30.12 1999 Total 3.39 36.62 40.01 High 0.56 29.88 30.44 Low 2.61 27.07 29.68 High Low 1.93 3.71 34.78 37.25 36.71 40.96 1997 Total 4.30 43.45 47.76 2002 Total 0.48 20.80 21.28 2000 High Low Total 2.55 5.91 3.81 43.11 43.77 45.65 49.68 42.02 45.82 High Low United Kingdom 2001 Total 0.38 0.45 13.91 21.52 27.89 14.29 21.97 2004 High 2.37 38.55 40.92 High Low 6.59 48.71 55.31 Low United States Total 3.98 47.98 51.95 2000 Total 0.65 25.92 30.73 High 3.13 48.88 52.01 Low 4.34 47.56 51.90 High Low 0.18 1.23 Note: Cell entries are percentages. Data are not weighted. 40 Table 2.2. NEP Non-Response and the Campaign: General Model NEPDK NEPMID NEPDKMID N Canada 1988 -0.0069 0.0050 -0.0024 0.0032 -0.0037 0.0030 3582 1993 -0.0032 0.0123 -0.0028 0.0034 -0.0029 0.0034 3775 1997 0.0045 0.0126 -0.0024 0.0036 -0.0016 0.0045 3949 2000 0.0028 0.0099 0.0046 0.0035 0.0049 0.0035 3651 2004 0.0180 0.0083 0.0023 0.0033 0.0049 0.0032 4323 New Zealand 1996 -0.0244 0.0131 0.0009 0.0048 -0.0024 0.0051 2103 1999 -0.0012 0.0128 -0.0019 0.0067 -0.0020 0.0064 1878 2002 -0.0340 0.0302 0.0033 0.0070 0.0026 0.0071 2514 United Kingdom 2001 0.0017 0.0023 4719 United States 2000 0.0029 0.0047 19507 Note: Main cell entries are logit coefficients. Robust standard errors below. Coefficients in bold significant at .05 or better. Table 2.3. NEP Non-Response and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication NEPDK NEPMID NEPDKMID N NEPDK NEPMID NEPDKMID N Canada 1988 -0.0087 -0.0043 -0.0056 1859 -0.0037 0.0013 0.0005 1711 0.0094 0.0046 0.0048 0.0067 0.0040 0.0042 1993 -0.0090 0.0006 0.0004 1255 -0.0054 -0.0055 -0.0059 2338 0.0322 0.0046 0.0046 0.0127 0.0041 0.0044 1997 -0.0010 -0.0071 -0.0071 1886 0.0082 0.0020 0.0038 2063 0.0158 0.0049 0.0057 0.0136 0.0053 0.0061 2000 -0.0039 0.0018 0.0014 2407 0.0068 0.0089 0.0103 1244 0.0153 0.0045 0.0044 0.0159 0.0070 0.0068 2004 0.0013 -0.0067 -0.0066 1342 0.0227 0.0059 0.0095 2975 0.0146 0.0050 0.0051 0.0110 0.0043 0.0043 New Zealand 1996 -0.0302 0.0153 0.0115 467 -0.0286 -0.0027 -0.0067 1549 0.0244 0.0123 0.0120 0.0148 0.0052 0.0057 1999 0.0022 -0.0092' -0.0089 369 -0.0031 0.0005 0.0000 1499 0.0380 0.0137 0.0141 0.0145 0.0090 0.0090 2002 -0.0428 0.0091 0.0082 532 -0.0528 0.0020 0.0006 1329 0.0302 0.0146 0.0144 0.0379 0.0067 0.0070 United Kingdom 2001 — 0.0048 0.0048 — 2743 — -0.0021 0.0051 — 1969 United States 2000 0.0150 0.0340 — — 3389 -0.0100 0.0086 — — 4148 Note: Main cell entries are logit estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. Figure 2.1. The Dynamics of Non-Response (DK) in National Economic Perceptions by Election Canada 1988 Canada 1993 Canada 1997 20 40 Day .. Canada 2000 T n - i — 0 " 20 40 60 Day •in o Canada 2004 -T "T ' 1— 20 40 60 Day New Zealand 1996 in o - i :—i— 20 40 Day 60 New Zealand 1999 New Zealand 2002 United States 2000 i n . ' i " " ' " " " " ' m 20 40 Day 20 40 Day 20 40 Day — i — 60 Note: Daily means smoothed by LOWESS, bandwidth=0.3. 4^ Figure 2.2. The Dynamics of Non-Response (DK + Middle) in National Economic Perceptions by Election Canada 1988 0 10 20 30 40 50 Day Canada 1993 CD -in --CO -0 10 20 30 40 5 0 Day Canada 1997 in co CM 0 1 0 . 20 3 0 40 50 • Day Canada 2000 CO CN4 0 10 20 30 40 50 Day Canada 2004 CO -in -rr. -co — ™ — • I I l 1 l l 0 10 20 30 40 50 Day New Zealand 1996 CO -in -"* -CO -CM -I I 1 I I ••• 1 -0 1 0 20 3 0 40 50 Day New Zealand 1999 co-J -I r|.......--.,|- I .|_. 0 • 10 20 30 40 50 Day New Zealand 2002 CD in CO I I — I I 1 •• • I - ' . 0 10 20 30 40 50 Day United Kingdom 2001 0 1 0 20 3 0 40 50 Day Note: Daily means smoothed by LOWESS, bandwidth=0.3. 4^ 44 CHAPTER THREE: THE DYNAMICS OF PERSONAL BIAS IN NATIONAL ECONOMIC PERCEPTIONS Voters' perceptions of the state of the national economy derive from sources both external and internal to the voter. Real changes in the economy are undoubtedly involved in economic judgement, along with the tone of economic news (Hetherington 1996; Haller and Norpoth 1996; Nadeau et al. 1999; Sanders and Gavin 2004). These are the principal external sources of national economic perceptions. The major internal sources include partisanship and perceptions of personal economic conditions (Weatherford 1983; Mutz 1992, 1994, 1998; Conover, Feldman and Knight 1986, 1987; Duch, Palmer and Anderson 2000; Johnston, Hagen and Jamieson 2004). Significantly, the relative balance of internal and external influences on economic judgement has clear implications for the quality of economic perception. Put simply, the objective validity of national economic perceptions is increasing in the impact of external forces on these perceptions.1 If election campaigns are truly 'enlightening' experiences, in the sense described in Chapter One, then the approach of Election Day should erode personal and partisan bias in economic perception across levels of political sophistication. Furthermore, an 'equalizing' campaign implies that the magnitude of 'bias reduction' should be inversely related to political sophistication level—that is, learning in the campaign should be greatest amongst the least informed. In this way, the chronically uninformed might hope to 'catch up' to the well informed over the course of the campaign. The pattern across the elections examined here turns out to be much more 1 As regards the impact of the media, this depends, of course, on economic news being representative of real conditions. 45 complex. Indeed, the real 'pattern' is, in fact, no pattern at all. Most of the time, the campaign has no apparent effect on the degree of personal or partisan bias in economic judgement, irrespective of the voter's level of political sophistication. When the campaign does have an impact, however, it is as likely to accentuate as to offset bias in national economic perceptions. Furthermore, there is no evidence of a consistent pattern of campaign effects across sophistication levels. Sometimes the campaign's effect is similar across levels—for instance, the campaign reduces bias among those both high and low on measures of political sophistication. At other times, however, the campaign seems to function differently across sophistication levels. In the most extreme case, the progress of the campaign reduces bias among the well informed but increases bias among the poorly informed. A l l this stands the enlightening-equalizing view of the campaign on its head, and leads to serious questions about key assumptions. For one thing, the findings suggest that the image of election campaigns as crucibles of political information, especially in the economic domain, needs to be carefully reconsidered. Indeed, the quality and quantity of campaign information may vary far more than is typically assumed. Generalizations about the motivating power of the campaign also seem questionable, as suggested in Chapter Two. Enticing though the drama of the campaign may seem, it may hold insufficient appeal to offset political inattentiveness among the politically unsophisticated. Thus, the campaign may not, in fact, supply voters with both the motivation and resources necessary to better-informed vote choices. The quality of the information may be more dubious and the motivating power of the contest less intense than is typically assumed. 46 The focus of the present chapter is the impact of the campaign on personal bias in national economic perceptions; the campaign's impact on partisan bias is the business of Chapter Four. The first step is a review of theoretical issues concerning personal effects in economic judgement. This is followed by a first cut at the analysis drawing on existing approaches. As it turns out, previous work suffers from serious methodological shortcomings, necessitating the development of an alternative approach. The heart of the chapter, accordingly, presents results derived from this alternative. A conclusion follows. T H E O R E T I C A L C O N T E X T If election campaigns supply voters with economic information, it seems obvious that the approach of Election Day should reduce personal bias in economic judgement. Yet existing theory suggests that the impact of the campaign depends crucially on the nature of personal bias—that is, how personal bias functions in psychological terms. Expectations about the impact of campaign information also depend on the nature of that information—on the quality of campaign economic discourse. Finally, the predicted impact of the campaign on the 'sophistication gap' also varies: the key assumption concerns the distribution of the campaign's effect across sophistication levels. This section canvasses the theoretical possibilities in each area, both alone and in combination. Personal Bias Personal effects in national economic perceptions (what is here termed personal bias) are conventionally understood to reflect the operation of an 'informational shortcut,' in the sense described in Chapter One. The argument is that, in the absence of information directly relevant to the formation of national economic perceptions, individuals make inferences from their personal economic circumstances to the state of 47 the national economy. Thus, for instance, those who have recently experienced a bout of unemployment or some other downturn in personal finances may be more likely than others to perceive national conditions as souring. The general proposition seems to have originated with Weatherford (1983); parallel findings are in Conover, Feldman and Knight (1986, 1987) and Mutz (1992). A key implication of this argument is that as one's store of directly relevant information—in this case, information about the state of national economic conditions— increases, reliance on the 'personal shortcut' should decline. As regards the impact of the campaign, then, if the campaign produces significant quantities of information that is diagnostic of national conditions, personal effects (personal bias) in economic judgement should decline with time in the campaign. A complication with this line of argument concerns the amount of information individuals require to make use of the personal shortcut in the first place. That is, the link between the personal and the political may not be obvious—it may require a non-trivial amount of framing discourse, as described in Chapter One, to make the connection. Findings in Mutz (1994) showing that personal effects maximize among the most informed support this view. Note the crucial implication for the impact of the campaign: the approach of election day may do as much to facilitate as to offset the link between personal economic conditions and national economic perceptions. The theoretical question is, thus, is the personal shortcut automatic or not? Campaign Economic Discourse In view of theory concerning the nature of personal bias, the nature of campaign economic discourse is obviously crucial to forming expectations about the campaign's 48 impact. Chapter One's distinction between raw data and framing discourse is relevant here. In the present context, recall that raw data means 'raw economic information': information concerning the objective state of the economy, although not necessarily 'objective' information. Raw data may even include 'episodic' depictions of personal economic hardship, such as reports of individual economic hardships or job losses in a particular industrial sector (Iyengar 1991). The important point is that this sort of discourse is the kind of directly relevant information for which, in its absence, individuals might substitute personal experience. Framing discourse, on the other hand, should facilitate just these kinds of substitutions. This is information that contains or encourages explicit links between personal economic experiences and national economic conditions. An archetypal example of such discourse would be a news report depicting the common experiences of economic hardship or success of a broad cross-section of individuals. As Mutz (1994) suggests, such discourse may help individuals to see their personal experiences as part of a "broader social pattern" (690) and, accordingly, may promote inferences from the personal to the collective.2 In practice, campaign economic discourse may contain a mixture of these two kinds of information. Indeed, a single 'unit' of campaign economic discourse—say, a report of recent job losses that portrays the experiences of displaced workers—may function as both raw data and framing discourse, by supplying information relevant to 2 Note the distinction between this argument and Mutz's (1998) argument that exposure to the "similar experiences" of others mainly promotes political accountability for personal experiences, rather than personal bias in perceptions of collective conditions (147-52). The distinction is important. Still, it seems likely that this sort of discourse helps to connect simultaneously both the personal and the political and the personal and the social. 49 national economic conditions while at the same time encouraging the view that one's personal experiences are part of a larger social process. The summary impact of the two kinds of discourse, providing the personal shortcut is non-automatic, may be nugatory: the two forces might offset each other, implying a campaign with no particular impact on personal bias in economic judgements. In any case, it is clear that expectations about the impact of the campaign are closely bound up with assumptions about the nature of campaign economic discourse. The Campaign and Voter Attention The final important area of theoretical variation concerns the campaign's impact on voter attention. The important arguments are covered in Chapter Two. Three plausible assumptions inform the analysis: First, the campaign has no impact on voter attention, leading to roughly equivalent effects across sophistication levels. Second, the campaign increases voter attention in equal amounts across sophistication levels, leading, again, to similar campaign effects across the electorate. And third, the campaign increases voter attention primarily among low sophistication voters, leading to maximum campaign effects within this group. Empirical Implications Now that the range of plausible assumptions about the nature of personal bias, the nature of campaign economic discourse, and the nature of the campaign's impact on voter attention have been reviewed, it is possible to consider the empirical implications of the interaction of these assumptions. This interaction is depicted in Table 3.1. Each cell of the table represents a combination of assumptions about the nature of personal bias, campaign economic discourse, and attention increases in the campaign. Cells contain 50 three predictions relevant to the analysis: the sophistication level with the highest initial personal bias in national economic perceptions (i.e. magnitude of partisan effect on the first day of the campaign); the relative magnitude of campaign effects across sophistication levels ('Equal,' greater among 'High' sophistication voters, greater among 'Low' sophistication voters); and the direction of the campaign's effect (+, -, 0). Each cell is also numbered for reference. Before treating specific predictions, note first some general points about Table 3.1. Although the table contains twelve combinations of assumptions, there are in fact just eight unique predictions. This creates obvious interpretive difficulties—the same results are compatible with different combinations of theoretical premises. Still, the table does reveal some important distinctions. In particular, no prediction is common across the automatic/non-automatic shortcut divide. Furthermore, as discussed below, those predictions that are duplicated within the table differ theoretically only in terms of one assumption—and that assumption never concerns the nature of personal bias. Consequently, the analysis is potentially instructive about theoretical conflict concerning personal effects in national economic perception. Now consider specific predictions: - Cells 1 and 5 depict the campaign's effect if personal bias functions as an automatic shortcut, the campaign's effect is evenly distributed across sophistication groups, and campaign economic discourse is constituted strictly by 'raw economic data' or is a combination of raw data and framing cues. In both cases, initial bias is maximized in the low sophistication group—as these individuals are initially most lacking in information directly relevant to national 51 economic perceptions—and bias declines to a similar degree across sophistication levels as the campaign progresses. As regards campaign economic discourse, the crucial fact is the presence of raw data, for which shortcutting is initially a substitute. The presence or absence of framing cues is irrelevant, for the personal shortcut is automatic in both cases. Cells 7 and 11 contain equivalent predictions to those for cells 1 and 5, but for the locus of the campaign's effect: attention increases are concentrated among low sophistication individuals and, consequently, so too is the campaign's effect. Cells 2 and 8 imagine the campaign's effect if personal bias is a non-automatic shortcut and campaign economic discourse is strictly populated by economic raw data. In both cases, initial bias is maximized in the high sophistication group—as these individuals are initially most likely to make links between personal and national economic conditions—and declines for all with the approach of Election Day. The one difference across the cells concerns the magnitude of effects across sophistication levels. Effects are symmetrical in cell 2 but asymmetrical in cell 8, as the concentration of attention increases among low sophistication individuals causes campaign effects to maximize in this group. Cells 3 and 9 portray the impact of the campaign if personal bias is an automatic shortcut and the campaign generates only framing cues. Whether attention increases are general, nil or concentrated in the low sophistication group, the prediction is the same: personal bias is initially greatest for low sophistication individuals and is unmoved by the campaign. Indeed, if the personal shortcut is truly automatic, as discussed with regard to cell 5, the presence of framing 52 information is irrelevant—individuals can make the appropriate links without the aid of the campaign. - Framing cues matter in cells 4 and 10, as here the personal shortcut is not automatic. Initial effects are greatest among high sophistication individuals and the progress of the campaign reinforces personal bias for all—the discourse of the campaign facilitates psychological links between personal and national economic conditions. Where attention increases are general or nil, as in cell 4, the campaign's impact should be similar across sophistication levels. If the motivating power of the campaign is concentrated in the low sophistication group, effects should be asymmetrical (cell 10). - Finally, cells 6 and 12 depict the campaign's impact if personal bias is a non-automatic shortcut and campaign economic discourse is a mixture of raw data and framing cues. Here, effects are initially greatest among the well informed and should be essentially unmoved by the campaign. This follows from the offsetting impact of campaign information under these conditions, as the presence of framing cues should facilitate shortcutting even as the intake of raw data reduces the need to do so. As it is for the null prediction in cells 3 and 9, the prediction here is the same regardless of the nature of the campaign's impact on attention. Which cells predict campaign learning? In the sense described in Chapter One, only cells 7 and 11 fit the bill. Here, shortcutting—that is, bias—is initially greatest among the uninformed and this 'bias gap' is reduced as the campaign proceeds. A l l other cells imply campaigns that are either 'non-learning' (e.g. the non-effects campaigns of cells 3, 9, 6 and 12), 'un-learning' (e.g. the bias-increasing campaigns of cells 4 and 10) 53 or just perverse (e.g. cell 8 implies a campaign that erodes bias among those who need it least—the uninformed—and, in so doing, increases the 'learning gap'). MEASURING PERSONAL ECONOMIC PERCEPTIONS The standard approach to the impact of personal economic perceptions (PEP) on perceptions of the national economy relies on respondents' perceptions of personal economic circumstances. The typical measure closely follows those addressed to national economic conditions. To parallel the measure of national economic perceptions, the PEP measure in the present analysis is retrospective where possible. A typical item is: • How does the financial situation of your household now compare with what it was 12 months ago? Has it got a lot better, got a little better, stayed the same, got a little worse, or got a lot worse? [BES 2001] A retrospective measure of this sort is missing from the NAES 2000—as with the NEP measure, a measure oriented to current economic conditions is substituted. Note also that data limitations force three elections from this part of the analysis—gone are New Zealand 1996, 1999 and 2002. These surveys lack campaign period measures of PEP of any kind. (The New Zealand cases return, however, when the analysis turns to objective measures; see below.) The distribution of personal economic perceptions across the seven remaining elections is presented in Table 3.2. (Note that 'don't knows' have been assigned middle values on the measure.) The table reflects the major source of wording variation across these measures—variation in the number of response categories. There are five response categories in the measures for Canada 1988 to 1997, four for the US in 2000 and three for 3 Exact question wordings appear in Appendix I. 54 Canada in 2000 and 2004. The consequences of this variation are discussed in Chapter Two in relation to the measurement of NEP. On the whole, however, the PEP measures are highly comparable. The modal response category in all but one of these elections is the middle one, corresponding to the perception that one's personal financial circumstances are "about the same" as they were a year earlier. The middling pattern is reflected in the PEP means across these elections, all of which cluster around 0.5. And this makes intuitive sense. Even dramatic macro-economic change seems likely to affect only a minority of the population in significant ways. The one exception to the pattern is Canada 1993—that year, the modal perception was of a worsening personal financial situation. But this may be the exception that proves the rule: the national economic situation during that election was dire indeed (see Chapter One). Even so, almost a third of Canadians felt that their financial condition was unchanged over the preceding year.4 Overall, then, the distribution of responses to PEP queries is sensible, at least when aggregated over the whole campaign. The implication is that personal economic perceptions reflect real conditions. Does the conclusion hold up when the distribution of PEP is examined over time? This is the business of the next section. PERSONAL ECONOMIC PERCEPTIONS AND THE CAMPAIGN If personal economic perceptions reflect real conditions, then the campaign should have no particular impact upon them. Voters have roughly as much information about their personal economic circumstances on the first as on the last day of the campaign. In the aggregate, this implies that personal economic perceptions are 4 Note that this occurred in spite of the fact that the 1993 item did not prompt for a middle response. See Appendix I. 55 essentially unmoved by the campaign. Large, secular shifts in economic conditions that register with precision over the short-term of the campaign might move PEP, but such shifts seem implausible. Normally, economic change unfolds slowly and impinges on different individuals at different times and in different degrees. Summed together these individual and various changes could be largely offsetting. The implication, then, is that the mean of personal economic perceptions is roughly constant over the campaign. The proposition is addressed in Figure 3.1, which plots mean PEP (smoothed) over the campaign for each of the seven elections for which the measure is available. The graphs also plot NEP means; these are addressed below. Focusing for the moment on the PEP means, it seems that the dynamics largely conform to expectations. In six of the seven elections, personal economic perceptions appear largely stable across the campaign. The plot for the US in 2000 is the standout in this regard—plotting mean PEP makes a straight line from Labour Day to Election Day. The one exception to the pattern of stability, however, unsettles the larger interpretation. In Canada in 2004, the plot suggests that personal economic perceptions moved roughly a tenth of the way across the range of the PEP measure over the campaign. The trend is strongly linear. It seems implausible that such a shift reflects real change in economic conditions during the campaign. This interpretation is buttressed by the fact that the PEP trend is nearly indistinguishable from the trend in national economic perceptions. The campaign seems to have supplied Canadian voters with crucial information on national economic conditions in 2004, information they had failed to acquire on their own. But there is no reason to expect the campaign to have supplied new information about personal economic conditions. This suggests that perceptions of 56 personal economic circumstances became interlaced with national economic perceptions as the campaign progressed. Closer inspection of the plots for the other elections finds a similar correspondence between dynamics in PEP and NEP. The clearest cases are Canada in 1993, 1997 and 2000, where ebb and flow in one measure is echoed by contemporary movement in the other. Parallel movements in the plots for the other elections are less discernible. Still, even in these cases PEP and NEP means are hardly dissimilar. The implications of all this are complex. The worst-case scenario is that personal economic perceptions are wholly endogenous to national ones—that voters do not, in fact, differentiate their economic perceptions as the political psychological models imply. A somewhat more hopeful—and plausible—interpretation is that the personal economic perceptions of some voters are elastic to national perceptions. An indication of this is in the plots for Canada from 1993 to 2000. Although the two measures seem to track each other in these elections, there is vertical distance between them. This implies that at least some voters differentiate the two perceptions: in 1993, for instance, many Canadians must have thought their personal economic situation was improving or about the same as in the previous year, even as they felt national conditions were worsening. For other voters, however, movements in the national economy—or in perceptions of the national economy—must be informing judgement of their personal financial situation.5 Crucially for the present chapter, if PEP is endogenous to NEP, then conventional 5 There is a certain wisdom in seeing the bearing of national conditions on one's personal economic situation. Even if one's current economic condition is unchanged—if one's income, savings and job situation are static—learning about changes in the national economy might reasonably alter expectations about one's future economic condition. PEP measures are, however, explicitly retrospective. The implication, then, is that the informational output of the campaign confounds, in some sense, personal economic perceptions with national ones. 57 statistical estimates of the impact of the campaign on the relationship between the two perceptions are biased. It matters less if the impact of NEP on PEP is constant over the campaign, but there is little reason to assume this is so. In fact, the campaign learning argument would seem to imply that any tendency of voters to generalize from the national to the personal would be heightened with the approach of Election Day—and so inversely correlated with any bias-reducing, negative relationship between campaign time and the PEP—>NEP link. The two effects would then be offsetting. Consequently, the analysis in the present chapter must be more indirect. For completeness, estimates of a dynamic model of the impact of personal economic perceptions on NEP are presented. Then, dynamics in the impact of two clearly exogenous, objective measures of personal economic circumstances—employment status and income—are examined. This permits sound inferences about the campaign dynamics of personal bias in NEP. 6 PERSONAL BIAS IN NATIONAL ECONOMIC PERCEPTIONS I The primary analytical strategy here is to regress, for each election, national economic perceptions on personal economic perceptions and interactions of these perceptions with campaign time, while controlling for important socio-demographics and party identification.7 If the perception-time interactions are negative and significant, then this implies that the campaign erodes personal bias in NEP. If the interactions are 6 Ideally, estimates of the impact of campaign time on the link between personal and national economic perceptions would deploy an instrument for one or the other perception. Unfortunately, the required identifying assumptions seem truly heroic in this case. That is, plausible determinants of PEP also tend to be plausible, direct determinants of NEP. 7 Models include socio-demographic variables derived from the work of the principal investigators of each election study. See Appendix I for details. 58 positive, however, this implies that the campaign increases personal bias in NEP. Two equations figure in the analysis: NEP =. f(Po + p ,P£P + (32DA7 + falNCPID + fi^OPID + ZfikSOCDEMk + u), (3.1) NEP = f(p\, + faPEP + f>2DAY + &PEP*DAY + ^NCPID + fi5INCPID*DAY + $eNOPlD + Z$kSOCDEMk + u), (3.2) where NEP = national economic perceptions; PEP = personal economic perceptions; DAY = day of campaign; INCPID = incumbent party identification (dummy); Q NOPID - no party identification (dummy); SOCDEMk = a set of socio-demographic variables (see appendix); and, u = random error. Equation 3.1 assumes that PEP effects are static over the campaign—the equation functions as a baseline of sorts. Equation 3.2 goes to the heart of the matter. The parameter of interest is 03, which quantifies the linear trend, if any, in the impact of personal economic perceptions on NEP over the campaign. Note that the equation also controls for campaign dynamics in the impact of partisanship on NEP by including the interaction INCPID*DAY (the measurement of party identification and the theoretical significance of these estimates is taken up in Chapter Four). The equations are estimated first for the whole of each sample, and then for sub-groups of the samples according to levels of political sophistication. Table 3.3 contains whole sample, OLS estimates of the parameters of interest.9 8 For the BES 2001 estimation, the variable pools those with no partisanship and those with non-major party identifications. 9 Full regression model results are contained in Appendix II. 59 The 'static model' confirms what seems obvious from the plots: there is a strong, positive relationship between PEP and NEP. Effects are substantively large and statistically significant in all of the elections. The median case is Canada in 2000, where a unit shift in PEP—that is, a move from the worst to the best perception of personal financial circumstances—improved perceptions of the national economy by roughly a fifth of the distance across the NEP scale. Effects for the US in that same year were twice as large— and also the largest in the table. Thus, leaving aside for the moment the endogeneity problem, personal bias in national economic perceptions would seem substantial indeed. Results for the 'dynamic model' go directly to the campaign learning argument— that personal bias in national economic perceptions declines with time in the campaign. In short, the hypothesis fails, at least according to this test. Coefficients on the PEP*DAY interaction (in the shaded area of the table) are indistinguishable from zero.1 0 Most estimates are substantively and statistically miniscule. Three coefficients would imply substantively significant dynamics in PEP effects over their respective campaigns— Canada 1988 and 2004, and U K 2001—but these estimates are far from conventional standards of statistical significance. And note that the estimates imply a 'framing' rather than 'learning' campaign: the coefficients imply increasing personal bias in national economic perceptions as the campaign unfolds. The main effects of personal economic perceptions are essentially undisturbed in these models, although standard errors are appropriately swelled. What if the samples are stratified by levels of political sophistication? Table 3.4 1 0 Note that the conclusion is robust to variation in model specification. If we drop the INCPID*DAY interaction from the model, which might confound estimates for PEP*DAY, effect estimates are almost identical. See Appendix II, Tables A2 to A9, Model 4. 60 presents estimates for high and low sophistication groups. Note first that the baseline impact of PEP across sophistication levels, as indicated in the static models, broadly comports with the expectations of Mutz (1994)—those high in political sophistication are typically more reliant than others on perceptions of their personal economic circumstances in the formation of national economic judgements, although in most cases the differences are very slight. This suggests that personal bias is a non-automatic shortcut. Turning to the dynamic models, the verdict is clear: across sophistication levels, the campaign has no significant impact on the magnitude or direction of personal bias in national economic perceptions. Nothing here disturbs the conclusions based on the general estimates. The campaign's apparent effect on the PEP—>NEP link is, thus, incompatible with the campaign learning argument. There is no tendency for the campaign to erode personal bias in economic judgement—indeed, the campaign might facilitate the link. Nor does the campaign tend to narrow the gap in the magnitude of personal bias across sophistication levels. Of course, the results in Tables 3.3 and 3.4 may be biased by endogeneity. As suggested above, the PEP—»NEP effect may be offset by an opposing NEP—»PEP effect of similar magnitude. Thus, a more decisive investigation of the dynamics of personal bias in NEP needs to employ indicators of PEP that are clearly exogenous to NEP. PERSONAL BIAS IN NATIONAL ECONOMIC PERCEPTIONS II As suggested above, two objective indicators of personal economic circumstances stand out as alternatives to the subjective measure: an indicator of (un)employment status and an income scale. The two variables have obvious implications for an individual's 61 current economic well being. Their bearing on change in an individual's economic circumstances—the focus of the retrospective personal economic perceptions query—is less clear. In principle, employment status and income level could be independent of employment status change and income change. Empirically, however, it is clear that personal economic perceptions are related to income and employment status.11 Furthermore, income and employment status effects on NEP are theoretically interesting in themselves. Notwithstanding the role of perceptions of personal economic change, campaign dynamics in the tendency of voters to default to their personal economic status in forming national economic judgements clearly speak to the campaign learning argument. The analytical strategy parallels that for the subjective measure of personal economic perceptions. Estimates are presented for two equations: NEP = f(p0 + pi UNEMP + ^INCOME + p 3 DAF + falNCPID + fcNOPID + ZpkSOCDEMk + u), (3.3) NEP = f(p0 + Pi UNEMP + ^INCOME + foDAY + p 4 UNEMP*DA Y + fi5INCOME*DAY + folNCPID + fi7INCPID*DAY + fcNOPID + T,pkSOCDEMk + u), (3.4) where NEP = national economic perceptions; INCOME = income scale (0-1); UNEMP - unemployed (dummy); DAY = day of campaign; INCPID = incumbent party identification (dummy); NOPID = no party identification12 (dummy); SOCDEMk = a set of socio-demographic variables (see appendix); and, ' 1 The magnitude of income and employment effects on NEP almost always drops when PEP effects are controlled. See Appendix II. 1 2 For the BES 2001 estimation, the variable pools those with no partisanship and those with non-major party identifications. 62 u = random error. Equation 3.3 is the baseline estimation here; equation 3.4 models any dynamics. As before, the dynamic model controls for any campaign effects on the impact of partisanship. Similarly, dynamics in one indicator of personal economic experience are estimated while controlling for dynamics in the other.13 Results for the unemployment models are treated first, followed by results for income. Unemployment Models: General Estimates Start with the general estimates, presented in Table 3.5. The 'static model' indicates that the overall impact of unemployment on NEP in these elections was quite sensible theoretically. In six of the ten elections the unemployed took a significantly less hopeful view of economic conditions than the employed, although the effects are fairly modest in terms of magnitude: from just 0.04 to 0.12. In the four remaining elections unemployment effects are indistinguishable from zero. Overall, however, the results suggest that national economic judgements were indeed subject to personal bias in most of these elections. What impact did the campaign have on the magnitude of this bias? In most cases, no impact at all, according to the estimates for the 'dynamic model'. In eight of the ten elections coefficient estimates for the interaction between unemployment and day of campaign are both substantively small and statistically insignificant. In the two remaining elections, however, the impact of the campaign appears significant. In Canada 2004 and New Zealand 1996 the progress of the campaign would seem to have increased the impact of unemployment on national economic perceptions. The effects are 1 3 No INCOME estimate is presented for U K 2001, as the available data lacks the requisite measure. 63 significant both statistically and in terms of substantive magnitude. The most dramatic effect is for Canada in 2004—the model suggests that the campaign turned a weak (and perverse) positive unemployment effect at the start of the campaign into a strong negative effect by Election Day (the shift is roughly from 0.08 to -0.22). The impact of the campaign in New Zealand in 1996 likewise turned a perverse positive effect into a modest negative one (the shift is roughly from 0.17 to -0.09). 1 4 In both of these elections, then, the impact of the campaign was to increase personal bias in national economic perceptions. Still, the overall pattern for unemployment suggests that the campaign's general impact is quite modest. Unemployment Models: Conditional Estimates As in the general estimates, unemployment effects on national economic perceptions for the static model when conditioning on sophistication level are quite sensible, if substantively small in most cases (see Table 3.6). 16 of the 20 estimates are appropriately negative and, of these, seven are statistically significant at conventional levels. The median among the statistically significant effects, for low sophistication respondents in the US in 2000, is -0.09—implying a difference in national economic perceptions between the employed and unemployed roughly a tenth the distance across the valid range of NEP. Curiously, one of the statistically significant effects is strongly positive: among high sophistication individuals in New Zealand in 1996, the unemployed are more positive about national economic conditions by roughly 0.20 units on the NEP scale. The perverse effect might reflect sampling variation, or it may reflect a certain 1 4 The initially positive effects of unemployment in these elections may be artefactual and could result from non-linearity in the campaign's over-time impact. For instance, unemployment effects could have been flat early in the campaign before a steep negative trend set in late in the campaign. Examination of this question is beyond the scope of the present analysis. 64 difficulty in linking unemployment to national economic perceptions (of this, more below). Comparing the magnitude of effects across levels suggests no particular pattern. Effects are quite similar across levels in three cases (Canada 1988-1997). In three others, the negative effect of unemployment is larger in the low sophistication group (Canada 2004, U K 2001, US 2000)—per the automatic shortcut view. In two cases, effects maximize among the sophisticated (Canada 2000 and New Zealand 1999)—per the non-automatic shortcut view. And, in the remaining two cases, the effect of unemployment is, perversely, positive among high sophistication voters and essentially nil among low sophistication voters (New Zealand 1996 and 2002). The diversity in the impact of political sophistication on unemployment effects bespeaks a larger pattern of heterogeneity in the campaign's effect, as discussed below. Suffice it to note that these findings countenance no simple conclusions concerning the nature of personal bias in national economic perceptions. Estimates for the dynamic models are similarly difficult to summarize. A first glance at the estimates suggests a striking pattern: the campaign decreases bias in the high sophistication group and increases it in the low sophistication group. A l l significant estimates of 04 (the coefficient on UNEMP*DAY in equation 3.4) among the sophisticated are positive (that is, they offset the negative effect of unemployment), while in the low sophistication group all such significant estimates are negative. Indeed, across all estimates, significant and otherwise, among high sophistication individuals, 3 of 10 estimates are negative, while in the low sophistication group that ratio rises to 8 to 10. The implications are clearly perverse from the campaign learning perspective: far from 65 offsetting pre-existing gaps in political learning, the campaign would seem to deepen them. However, this interpretation is too hasty. Understanding the substantive significance of these apparent dynamics depends pivotally on where unemployment effects start, as suggested by the theoretical analysis in Table 3.1. For this purpose, it is helpful to plot the campaign dynamics. Unemployment Models: Interpreting the Dynamics The plots in Figure 3.2 are designed to speak to the structure of the predictions contained in Table 3.1. They depict, for each election, the estimated linear impact of campaign time on the magnitude of unemployment effects in.national economic perceptions by sophistication level. Thus, at a glance, it is possible to see the group in which the initial effect is maximized, the direction of the campaign's impact on the nature of unemployment effects, and the relative magnitude of the campaign's effect across sophistication levels.1 5 What do the plots imply for the chapter's major research questions? First, there is no general tendency for the campaign to erode personal bias in national economic perceptions. In just three elections (Canada 1997, New Zealand 1999 and US 2000) did the campaign reduce bias to a substantively significant degree, and even then, the reduction occurred only among high sophistication individuals. In three other elections, the campaign would seem to have magnified personal bias—among low sophistication individuals in Canada 1988 and 2004, and among high and low sophistication individuals in Canada 1993. In two cases, the impact of the campaign was to erode a perverse—that 1 5 A l l the plots are on a common scale, save for New Zealand 1996, where the range of effects demands that the range of the y-axis be increased. is, a positive—unemployment effect among low sophistication individuals (New Zealand 1996 and 1999). The campaign had the opposite effect in two other cases: massive positive unemployment effects emerge by Election Day among the sophisticated in New Zealand in 1996 and 2002. Finally, in two elections, the campaign seems to have produced no significant dynamics of any kind (Canada 2000, U K 2001). In short, the campaign is as likely to increase as offset personal bias in national economic perceptions—that is, when the campaign has any effect at all. The campaign's impact on pre-existing gaps in the magnitude of personal bias across sophistication groups is similarly troubling to campaign learning expectations. In only one election, New Zealand 1999, does the campaign seem to have narrowed the gap, but it did so in an unexpected way: by simultaneously reducing a perverse positive unemployment effect in the low sophistication group and a more theoretically sensible negative unemployment effect in the high sophistication group; by election day, both effects were close to nil. The modal result, however, is for the campaign to have essentially no impact on the sophistication gap—this was the case in six elections (Canada 1988 to 2000, U K 2001, US 2000). In the remaining two elections, the campaign actually magnified differences across sophistication groups (Canada 2004 and New Zealand 2002). Overall, then, the results offer little reason to credit the campaign learning argument. Most of the time, the campaign has no appreciable impact—in both statistical and substantive terms—on the magnitude of unemployment effects in national economic perceptions. When the campaign does matter, it is roughly as likely to grow as shrink personal bias in economic judgement. And, consequently, the campaign typically has no detectable effect on pre-existing gaps in the magnitude of personal bias across 67 sophistication groups. Campaign learning arguments aside, how do the results square with the theoretical expectations outlined in Table 3.1? Only one election clearly fits a theoretically interpretable pattern: in Canada 2000, unemployment effects are maximized in the high sophistication group and are essentially unmoved by the campaign. Such a pattern follows from the assumptions in cells 6 and 12—personal bias is a non-automatic shortcut and campaign economic discourse is a mixture of economic raw data and framing cues and, consequently, the campaign produces offsetting effects. One other election approximates theoretical assumptions: the parallel increases in unemployment effects in Canada 1993 echo the expectations of cell 4, which define the case where personal bias is a non-automatic shortcut and the campaign produces framing cues and general increases in political attention; the results differ only in the very modest initial asymmetry of unemployment effects across sophistication groups. Apart from these two elections, however, the results are essentially uninterpretable in view of standard assumptions. For instance, United Kingdom 2001, as noted above, witnessed no significant movement in unemployment effects over the campaign, and the initial magnitude of effects was quite symmetrical. These results square with none of the theoretical possibilities in Table 3.1. Results for the US 2000—where the campaign eroded personal bias in the high sophistication group while leaving effects in the low sophistication group undisturbed—are similarly uninterpretable. The strangest patterns, however, are in results for New Zealand. In 1996, the campaign produced a positive unemployment effect in the high sophistication group while eroding a similarly positive, if relatively 68 modest, effect in the low sophistication group. This pattern is clearly perverse; no plausible interpretation suggests itself. Results for 2002 are similar: the campaign created a perverse effect in the high sophistication group, while effects in the low sophistication group were essentially static (and very modest, in any case). New Zealand 1999—the one 'gap reducing' election—might be the strangest of the lot: as discussed above, the campaign offset both a positive effect among the uninformed and a negative effect among the informed, such that unemployment effects were close to nil by election day. None of this comports with any obvious theoretical interpretation. Results for the three remaining elections, however, are more theoretically suggestive. In particular, the pattern in Canada 1988, 1997 and 2004 hints at the possible importance of cognitive heterogeneity in understanding the impact of the campaign. In each of these cases, the campaign increased unemployment effects in the low sophistication group while effects in the high sophistication group either decreased (1997) or were static (1988, 2004). One theoretical possibility, then, is that the campaign has different effects across sophistication levels. In particular, the campaign may supply low sophistication voters with sufficient motivation and framing cues to make use of shortcuts, at the same time as it motivates high sophistication voters to pay careful attention to raw economic data, which may be more cognitively demanding in any case. As suggested in Chapter One, such a view seems compatible with dual process theories of information processing in social psychology (e.g. Petty and Cacioppo 1986). In any case, the implication for these three elections is that the campaign may have had different effects on different individuals—enabling the uninformed to make use of shortcuts, while permitting the informed either to combine shortcutting with raw data (producing 69 offsetting dynamics in Canada 1988 and 2004) or to forgo shortcutting entirely (producing the negative dynamic in Canada 1997). Nevertheless, it remains that most of these results are uninterpretable in light of existing theory. Some results are truly perverse (the three New Zealand elections), while others suggest profound revisions to the standard assumptions (Canada 1988, 1997 and 2004). As regards the campaign learning perspective, conclusions can be more summary: There is no evidence of a general tendency for the campaign to erode the magnitude of personal bias in national economic perceptions. Furthermore, there is no evidence of a general tendency for the campaign to narrow the gap between high and low sophistication individuals in the degree of personal bias in national economic perceptions. Income Models: General Estimates Do conclusions differ based on the income models? Table 3.7 presents general estimates of income effects on national economic judgements. Results for the static model indicate that in all but one case the impact of income is significant and sensibly positive. The magnitude of effects varies somewhat, but most effects are substantively large. The implication is that, in line with the analysis of unemployment effects, personal bias in national economic perceptions rooted in income levels was significant in almost all of these elections. As regards campaign dynamics, the results suggest that, for the most part, the campaign appears to have no impact at all, but when it does have an impact, it is to increase personal bias in national economic perceptions. Estimates for three elections imply increasing income effects in national economic perceptions as the campaign progresses: Canada 1993 and 2004, and New Zealand 1996. The most striking shift is for 70 New Zealand in 1996, where the impact of a unit shift on the income measure grew from roughly nil to 0.19 between the first and last days of that campaign. Shifts in the other two elections were also sizeable, if not quite so dramatic (from - 0.03 to 0.11 and from 0.06 to 0.17 in Canada 1993 and 2004, respectively). For the remaining six elections, the campaign effects are not significant. From the perspective of campaign learning, then, these results suggest that the campaign's impact is nugatory at best, bias-increasing at worst. Income Models: Conditional Estimates Stratifying effects by sophistication levels hardly improves the case for the campaign learning argument, as depicted in Table 3.8. Note first that, unlike the results for unemployment effects, income effects tend to be quite uniform across sophistication levels, at least as rendered in the static models: whenever income effects are significant, they are significant at both high and low levels of political sophistication. Effects are moderately larger among the sophisticated in two cases, but are otherwise quite similar across sophistication levels. Thus, income would seem neither a default source of economic judgement for the uninformed or a unique source of economic information for the well informed—the shortcut is useful and accessible across levels of political sophistication. As regards campaign effects, however, results are less uniform across sophistication levels. Three of the four significant effects are found among low sophistication voters—in Canada 1988 and New Zealand 1996 and 2002. Two of these effects are of the bias-increasing variety: in Canada 1988 and New Zealand 1996 the campaign produced large increases in income effects in the low sophistication group. In 71 New Zealand 2002, by contrast, the campaign seems to have had an opposite effect on low sophistication voters: a negative trend in income effects over the campaign produces a perverse, if moderate, negative income effect on national economic perceptions by election day. The one significant campaign effect among high sophistication voters is for Canada 2004, where the progress of the campaign produced a massive increase in income effects. Income Models: Interpreting the Dynamics As for the unemployment models, decisive evaluation of the chapter's principal research questions demands that the dynamics of income effects in national economic perception be plotted. Accordingly, Figure 3.3 is directly modelled on Figure 3.2. First, is there any evidence that the campaign erodes income effects—i.e. that it reduces personal bias in national economic perceptions? In general, the answer to this question is no. Eight of the eighteen slopes in the figure imply no significant movement whatsoever—by either statistical or substantive standards. Seven other slopes are clearly positive, that is, they imply bias increasing campaigns. Just three slopes imply bias reducing campaigns. In short, just as for unemployment effects, there is no general tendency for the campaign to erode income effects. More commonly, the campaign either increases income effects or has no particular impact upon them. What about the 'sophistication gap'? Does the campaign reduce differences across sophistication groups in the magnitude of income effects? Here again, the answer is no. In fact, in only one election—New Zealand 2002—is there even a hint that the campaign has such an effect and, even in this case, the dynamics are perverse.16 1 6 Income effects crash to a nullity in the low sophistication group, at the same time as they increase from a perverse negative effect to a moderately positive effect in the high sophistication group. 72 Elsewhere, the campaign has no appreciable impact on the gap between low and high sophistication individuals—a gap that is, in any case, generally quite small. These results, then, together with those for the unemployment models, leave the campaign learning argument very much in doubt. That said, in contrast to the unemployment results, results for income are much more interpretable theoretically. Seven of the nine elections in the income analysis fit or approximate some combination of the theoretical assumptions outlined in Table 3.1. Furthermore, none of these seven lends credence to the automatic shortcut interpretation of personal bias—that is, all of the elections suggest that income effects on national economic perception are a non-automatic shortcut. The important variation across these elections, it would seem, is in the nature of campaign economic discourse. Take, for instance, results for New Zealand 1996: income effects are initially greatest for high sophistication individuals but increase in the campaign across sophistication levels, especially in the low sophistication group. This pattern fits the expectations of cell 10, which imagines a campaign wherein personal bias is a non-automatic shortcut, economic discourse is constituted by framing cues, and attention increases are concentrated in the low sophistication group. Canada 1988 and 1993 approximate the similar expectations of cell 4 (which differs from cell 10 only in the fact that attention increases are general or nil, rather than asymmetrical), except that the magnitude of initial income effects is quite similar across sophistication levels. A quite different pattern of effects, although also supportive of the view that personal bias is a non-automatic shortcut, is found in New Zealand 1999. Here, income effects, which are initially greatest among the well informed, decline over the course of the campaign 73 irrespective of sophistication level. This fits the expectations of cell 2, which depicts the campaign's impact if personal bias is a non-automatic shortcut, campaign economic discourse is constituted by economic raw data, and attention increases in the campaign are general or nil. Finally, three elections approximate, to varying degrees, the expectations of cells 6 and 12—the predicted impact of the campaign if personal bias is a non-automatic shortcut and campaign economic discourse is a mixture of raw data and framing cues. The non-dynamics in income effects for Canada 1997 and 2000 and US 2000 fit the expectation of offsetting effects under these conditions, excepting that, in the latter two elections, initial differences in income effects across sophistication levels are negligible. Details aside, then, results for these seven elections strongly imply that personal bias—or, at least, income effects—are not automatic: the campaign supplies a non-trivial amount of framing or linking information that permits individuals to connect their personal economic condition to national economic judgement. Furthermore, variation in the nature of the campaign's effect across elections might plausibly be said to reflect variation in the nature of campaign economic discourse—specifically, the relative salience of economic raw data and framing cues in campaign communications. Results for the two remaining elections are not interpretable in light of existing theory. Most unusual are results for New Zealand 2002, where effects crash to a nullity in the low sophistication group, at the same time as they increase from perversely negative to moderately positive in the high sophistication group. Similarly unintepretable are results for Canada 2004, where, as noted above, income effects grew dramatically for high sophistication individuals, even as effects were stable in the low sophistication 74 group. These anomalies aside, the income results are quite interpretable theoretically—at least relative to the results for the unemployment models. To be sure, nothing here squares with the conventional wisdom encapsulated in the campaign learning argument: the quality of national economic perceptions and gaps in the quality of those perceptions across sophistication groups seem little affected by the progress of the campaign. Still, in contrast to the results for the unemployment models, results for income are quite instructive. C O N C L U S I O N The analysis in this chapter suggests serious revisions to the conventional wisdom about the impact of election campaigns on political learning. Most fundamentally, the results strikingly contradict the standard view that the campaign is a learning experience for the voter. The most common finding is for the campaign to have no particular effect on the quality of national economic perceptions—the campaign leaves personal biases intact and does little to offset pre-existing gaps in the magnitude of personal biases across sophistication groups. Furthermore, when the campaign does have a detectable effect, it is more likely to increase than decrease bias in economic judgement and gaps in the quality of those judgements across the electorate. The safest generalization about the impact of the campaign, then, would seem to be the following: most of the time the campaign has no net impact on the quality of national economic perceptions, but when the campaign does matter, it is more likely to undermine than promote quality economic judgement. What are null findings from the campaign learning perspective, however, have 75 important, if equivocal, theoretical implications. For one thing, the image of personal effects in national economic perception as an 'automatic shortcut' appears seriously misguided. Across the results for the three measures of personal economic condition considered in this chapter, one commonality is the presence of evidence in support of the 'non-automatic shortcut' view. The key results concern income effects, where dynamics in almost all elections comport with the conception of personal bias as a non-automatic shortcut, albeit under varying discursive conditions. Furthermore, in no case—across the personal economic perceptions, unemployment and income models—are there dynamics that fit automatic shortcut expectations. Comparing the overall pattern of results for the unemployment models with the results for the income models also lends credence to the non-automatic shortcut perspective. Recall that unemployment effects are, in general, smaller, less consistent and less theoretically interpretable than those for the income models. If the link between personal and national economic conditions depends on seeing one's own situation as part of a 'broader social process,' per Mutz, it makes sense that income effects should eclipse unemployment effects. Membership in a given income category should be a relatively stable condition, one that is at least somewhat predictive of a host of social, economic and cultural experiences. In contrast, unemployment is typically a temporary condition, and the unemployed population is presumably crosscut by a range of politically significant cleavages (including, for example, income). Accordingly, it seems likely that it is easier to conceive of oneself as a member of a broad group of income earners than a broad group of unemployed persons. The contrast underlines the non-automatic nature of the personal-national link in economic perception: the connection is mediated by a host 76 of factors—social, economic, political—that govern the cognitive accessibility of different interpretations of reality. The nature of the personal shortcut in national economic perception aside, results for unemployment in a handful of the elections also hint at deeper theoretical possibilities, as noted above. In particular, evidence that the campaign may have different effects across sophistication groups—that it might erode bias among the informed and create bias among the uninformed—raises the possibility that the campaign creates cognitive heterogeneity across the electorate. That is, the campaign may supply just enough motivation and information to encourage shortcutting in the low sophistication group, even as it facilitates more intense, "central processing" (Petty and Cacioppo 1986) in the high sophistication group. The suggestion encourages more subtle expectations regarding campaign learning. Indeed, it might be that the campaign motivates the information rich to become cognitive sophisticates, while at the same time raising the information poor from cognitive pauperism to mere cognitive miser-hood. 77 Table 3.1. Predicted Campaign Effects by Theoretical Assumptions Campaign Economic Discourse Raw Data Framing Mixed Personal Bias/ Attention Increases Automatic Shortcut Non-Automatic Shortcut Automatic Shortcut Non-Automatic Shortcut Automatic Shortcut Non-Automatic Shortcut General or Nil (1) Low, Equal, (2) High, Equal, (3) Low, Equal, 0 (4) High, Equal, + (5) Low, Equal, (6) High, Equal, 0 Low Soph. Only (7) Low, Low, (8) High, Low, (9) Low, Equal, 0 (10) High, Low, + (11) Low, Low, (12) High, Equal, 0 Note: Cell entries indicate predicted (i) sophistication level with highest initial effect, (ii) relative magnitude of effects across sophistication levels, and (iii) direction of effect. 78 Table 3.2. PEP by Election 0 .25 .5 .75 1 Mean /V Canada 1988 6.48 15.66 39.84 28.51 9.50 0.547 3609 1993 14.91 34.04 28.26 17.40 5.38 0.411 3775 1997 10.08 20.13 52.47 11.40 5.93 0.457 3949 2000 19.80 — 56.59 — 23.61 0.519 3651 2004 25.68 — 55.26 — 19.06 0.467 4323 United Kingdom 2001 7.35 15.07 40.54 26.54 10.50 0.544 4751 .33 .66 Mean N United States 2000 7.97 29.70 0.54 51.40 10.40 0.548 19507 Note: Unweighted data. 79 Table 3.3. PEP Effects on NEP and the Campaign: General Estimates Static Model PEP Dynamic Model PEP PEP* DAY N Canada 1988 0.1348 0.0160 0.0953 0.0343 0.0016 0.001 I 2803 1993 0.1524 0.0187 0.1508 0.0400 0.0001 0.0016 3004 1997 0.2484 0.0313 0.2502 0.0635 -0.0001 0.0029 3157 2000 0.2023 0.0211 0.1997 0.0393 0.0001 ().()()22 3026 2004 United Kingdom 2001 United States 2000 0.1803 0.0207 0.2378 0.0177 0.3891 0.0082 0.1475 0.0570 0.2054 0.0315 0.3838 0.0200 0.0017 . v 0.0023 0.0021 0.0023 0.0002 0.0005 3519 4550 17382 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at. 10 or better. Table 3.4. PEP Effects on NEP and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication Static Model Dynamic Model Static Model Dynamic Model PEP PEP PEP*DAY N PEP PEP PEP*DAY N Canada 1988 0.1565 0.1370 0.0007 1524 0.1183 0.0685 0.0022 1273 0.0242 0.0493 0.0018 0.0262 0.0508 .0.0017 1993 0.1390 0.0821 0.0026 1088 0.1559 0.1984 -0.0017 1767 0.0268 0.0429 0.00IO 0.0231 0.0526 0 0018 1997 0.2525 0.1724 0.0040 1577 0.2431 0.3204 -0.0042 1580 0.0450 0.0918 / 0.0037 0.0422 0.0837 -, 0.0042 2000 0.2071 0.1963 0.0005 2069 0.1885 0.2275 -0.0020 957 0.0298 0.0544 0 0029 0.0382 0.0837 0.0041 2004 0.1988 0.2017 -0.0002 1132 0.1756 0.1232 0.0027 2386 0.0285 0.0838 , '^-•0.00 ' 2 0.0273 0.0612 0 0026 United Kingdom 2001 0.2578 0.2035 0.0035 2660 0.1943 0.1835 0.0007 1883 0.0238 0.0486 o oir -o 0.0238 0.0474 n.oo:x United States 2000 0.3687 0.3910 -0.0006 3112 0.4184 0.3797 -.j .0.0010 3609 0.0206 0.0684 0 0017 0.0192 0.0536 0.0012 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. 81 Table 3.5. Unemployment Effects on NEP and the Campaign: Genl. Estimates Static Model UNEMP Dynamic Model UNEMP UNEMP *DAY N Canada 1988 1993 -0.0227 0.0149 -0.0477 0.0196 0.0103 0.0284 -0.0118 0.0428 -0.0014 i 0.0009 -0.0015" 0.0015 2803 3004 1997 2000 2004 New Zealand 1996 -0.1194 0.0275 -0.0548 0.0297 -0.0762 0.0309 -0.0017 0.0627 -0.1168 0.0694 -0.0411 0.0633 0.0752 0.0514 0.1699^ 0.0921 -0.0001 0.0028 -0.0007 0.0031 -0.0083 0.0034 -0.0069 0.0038 3157 3026 3519 1328 1999 2002 0.0171 0.0265 0.0077 0.0329 0.0790 0.0495 0.0050 0.0551 -0.0036 0.0026 0.0006 0.0034 1180 1485 i l l United Kingdom 2001 United States 2000 -0.0649 0.0219 -0.0415 0.0167 -0.0625 0.0499 -0.0341 0.0349 0.00O" 0.0030 -0.0002 0.0009 4550 17382 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at. 10 or better. Table 3.6. Unemployment Effects on NEP and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication Static Model UNEMP Dynamic Model UNEMP* UNEMP DAY N Static Model UNEMP Dynamic Model UNEMP* UNEMP DAY N Canada 1988 -0.0296 -0.0475 0.0007 1524 -0.0202 0.0514 -0.0032 1273 0.0182 0.0438 0 H0I3 0.0233 0.0420 (10015 1993 -0.0431 -0.0065 -0.0018 1088 -0.0479 -0.0045 -0.0018 1767 0.0451 0.0967 O.D034 0.0213 0.0360 0.0014 1997 -0.1281 -0.2491 0.0056 1577 -0.1015 -0.0626 -0.0020 1580 0.0563 0.1769 0.0073 0.0307 0.0717 0.0030 2000 -0.0995 -0.0764 -0.001 \ 2069 -0.0001 0.0188 -0.0009'." 957 0.0430 0.0870 0 0043 0.0396 0.1133 0.0053 2004 0.0215 0.0744 -0.002S 1132 -0.0786 0.0899 -0.0091 2386 0.0781 0.1442 0 0045 0.0314 0.0469 n.rxni New Zealand 1996 0.1891 -0.5106 (I.03IK, 333 -0.0109 0.1351 -0.1)061 942 0.0937 0.3668 0.0143 0.0629 0.0778 0.IM)33 1999 -0.1267 -0.3193 0.0102 219 0.03.77 0.1269 -0.0053 952 0.1220 0.1728 0 01(12 0.0247 0.0395 -,.;.-aooi9 •' 2002 0.0761 -0.1049 0.0117 366 -0.0130 0.0208 -0.0017 1013 0.0908 0.0617 o.nofix 0.0294 0.0626 0 0031 United Kingdom 2001 -0.0157 -0.0966 0.0052 2679 -0.0761 -0.0802 •0.0003 ' ; 1916 0.0322 0.0568 DOOM 0.0248 0.0492 0.0028 United States 2000 -0.0628 -0.2411 0.0047 3112 -0.0933 -0.1042 • 0.0003 " 3609 0.0411 0.0891 0.0021 0.0307 0.0801 0.0019 -Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. 83 Table 3.7. Income Effects on NEP and the Campaign: General Model Static Model Dynamic Model INCOME INCOME INCOME *DAY N Canada 1988 1993 1997 0.0537 0.0158 0.0450 0.0192 0.1582 0.0347 0.0138 0.0285 -0.0309 0.0439 0.1418 0.0728 0.0016 ! 0.0011 0.0032 0.0015 0.0008 0.0031 2803 3004 3157 2000 2004 New Zealand 1996 1999 0.1254 0.0226 0.1192 0.0166 0.0972 0.0360 0.1323 0.0322 0.1176 0.0400 0.0613 0.0315 0.0052 0.0599 0.1874 0.0551 0.0004 0.0017 0.0030 > 0.00 I ft 0.0050 0.0026 -0.0035 - ] 0.0022 ' I 3026 3519 1328 1180 2002 United States 2000 0.0184 0.0326 0.2646 0.0084 0.0849 0.0631 0.2794 0.0171 ^0.0038 0.0027 -0.0005 0.0005 1485 17382 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at. 10 or better. Table 3.8. Income Effects on NEP and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication Static Model Dynamic Model Static Model Dynamic Model INCOME* INCOME* INCOME INCOME DAY N INCOME INCOME DAY N Canada 1988 0.0432 0.0145 1524 0.0556 -0.0014 0.0024 1273 0 . 0 2 1 0 0 . 0 4 4 2 0 . 0 0 1 h 0 . 0 2 1 2 0 . 0 3 4 5 0 . 0 0 1 4 1993 0.0467 -0.0199 0.0030 1088 0.0325 -0.0214 0.0021 1767 0 . 0 3 5 8 0 . 0 6 7 2 . 0 . 0 0 2 2 0 . 0 1 9 6 0 . 0 4 0 7 j.V * 0 . 0 0 1 5 1997 0.1661 0.1589 0.0003 , 1577 0.1128 0.0871 0.0013 1580 0 . 0 3 7 6 0 . 0 6 8 0 O O O V i 0 . 0 4 5 1 0 . 0 8 6 0 0 . 0 0 3 8 2000 0.0961 0.0926 0.0001 2069 0.0909 0.0985 -0.0004 957 0 . 0 2 1 4 0 . 0 3 6 9 0 . 0 0 1 7 0 . 0 5 3 4 0 . 1 2 9 2 0 . 0 0 5 8 2004 0.0884 -0.0639 0.0078 1132 0.1058 0.0954 0.0006 2386 0 . 0 4 0 6 0 . 0 6 7 0 0 . 0 0 ' 1 0 . 0 2 1 5 0 . 0 3 9 5 O . D 0 I 7 New Zealand 1996 0.1591 0.1084 0 0027 333 0.0944 0.0040 0.0049 ( 1 . 0 0 2 9 942 0 . 0 5 6 4 0 . 0 8 8 9 ' , . 0 . 0 0 4 5 0 . 0 4 1 7 0 . 0 7 1 1 1999 0.1545 0.2360 -0.0046 219 0.1231 0.1798 -0.0036 952 0 . 0 8 1 1 0 . 1 5 5 9 0 . 0 0 S 1 0 . 0 3 2 4 0 . 0 5 6 4 0 . 0 0 2 4 2002 -0.0357 -0.1151 0.0042 366 0.0347 0.1395 >>V,^ 0.006(K. 1013 0 . 0 6 0 7 0 . 1 1 7 9 0 . 0 0 5 8 0 . 0 4 6 3 0 . 0 8 1 1 p ' ; 0 . 0 0 3 6 United States 2000 0.2409 0.2127 0.0007 3112 0.2450 0.2536 -0.0002 3609 0 . 0 2 2 2 0 . 0 6 3 8 0 0(11 > 0 . 0 2 2 2 0 . 0 7 3 4 0 . 0 0 1 h Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. Figure 3.1. The Dynamics of Personal (PEP) and National Economic Perceptions (NEP) by Election Canada 1988 CD 20 40 Day . 60 1 ;^ CD in co Canada 1993 20 40 - Day,., 60 CD 10 "* -I CO Canada 1997 20 40 Day 60 ^ 4 CD If) CO Canada 2000 20 „ 40 ••• 60 • Day -cq -CO -Canada 2004 — i T — 20 40 Day — i — 60 United Kingdom 2001 I V . . CD . If) . CO . 20 . 40 -'• ' Day, V-;:. 60 United States 2000 CD , IO. •<*, CO, 0 20 4 0 60 ; •  Day > Note: Daily means smoothed by LOWESS, bandwidth=0.3. Solid line = PEP; Dotted line = NEP. CO Figure 3.2. Dynamics of Unemployment Effects in NEP by Sophistication Level by Election oo ON Figure 3.3. Dynamics of Income Effects in N E P by Sophistication Level by Election oo —i 88 CHAPTER FOUR: THE DYNAMICS OF PARTISAN BIAS IN NATIONAL ECONOMIC PERCEPTIONS Evidence for the impact of party identification on political perception is legion (e.g. Lazarsfeld, Berelson and Gaudet 1944; Berelson, Lazarsfeld and McPhee 1954; Campbell, Converse, Miller and Stokes 1960, 1966; Markus and Converse 1979; Franklin and Jackson 1983; Lodge and Hamill 1986; Jacoby 1988; Conover and Feldman 1989; Rahn 1993; Finkel 1993; Granberg 1993; Bartels 2002; but see Gerber and Green 1999; Krosnick 2002). Work concerning the impact of partisanship on economic perception is somewhat less plentiful, although still commonplace (Kinder and Mebane 1993; Conover, Feldman and Knight 1987; Mutz 1994; Duch, Palmer and Anderson 2000; Johnston, Hagen and Jamieson 2004). And in this regard, the conventional wisdom is clear: perceptions of national economic conditions are biased by partisan inclinations. For arguments concerning accountability and economic voting, this persistent bias has troubling implications. In short, if voters' perceptions of the economy are biased by pre-existing partisan commitments, then voters' ability to hold governments to account for changes in real economic conditions is compromised. An election campaign that facilitates political learning should offset this dynamic. As for personal bias, an 'enlightening' and 'equalizing' campaign should have two effects on partisan bias in national economic perceptions: First, the approach of Election Day should erode partisan bias across the electorate, that is, across levels of political sophistication. In this way, the campaign might be said to 'enlighten' the electorate. Second, the progress of the campaign should 'narrow the gap' between those at high and 89 low levels of sophistication. Specifically, assuming partisan bias is maximized among the uninformed, the magnitude of bias reduction should be negatively related to sophistication level. In this way, the campaign might be said to 'equalize' political learning across the electorate. The aim of the present chapter is to evaluate this campaign learning argument. As it happens, theory regarding the impact of party identification on economic perception provides only mixed guidance for such an inquiry. Expectations vary depending on assumptions about the nature of partisan bias, the nature and function of discourse about the economy, and the nature of the campaign's impact on voter attention to economic discourse. As a result, theory yields multiple predictions regarding the campaign dynamics of partisan bias in national economic perceptions—some conflicting, some overlapping. The consequence is a certain theoretical confusion about the campaign's effect. Still, the chapter comes to some decisive conclusions, especially as regards campaign learning. Put simply, the evidence for the enlightening-equalizing view of campaigns is almost nil. Most of the time, the campaign has no apparent effect on partisan bias. But, when it does have an effect, it is as likely to increase as offset partisan bias in national economic perceptions. Worse, bias increases may be confined to low sophistication voters. Indeed, at times the campaign would seem to increase bias among low sophistication voters at the same time as it decreases bias among high sophistication voters. This is a perversion of the equalization hypotheses: the campaign can make the information rich richer and the information poor poorer. Theoretical implications are somewhat murkier, but one finding seems clear: 90 campaign information in the economic,domain does not simply function as 'raw data' about real conditions that substitutes for inferences from partisan commitment. This view misses an important fact about partisanship and economic perception: the link between the political and the economic is not obvious; voters require a non-trivial amount of framing or linking information to know the economic implications of partisanship. In other words, voters must learn to take a more (less) positive view of economic conditions when their party is in (out of) office.1 The informational onslaught of the campaign, thus, need not reduce the likelihood of partisan inference or bias in economic perception. On the contrary, the campaign may facilitate such processes. Apart from this conclusion, however, the data are compatible with a range of assumptions about the psychology of partisan bias, campaign economic discourse, and the campaign's impact on voter attention. The chapter begins with a review of the theoretical terrain. This is followed by treatment of methodological issues and detailed discussion of results. A conclusion follows. T H E O R E T I C A L C O N T E X T As noted in the introduction, theoretical expectations regarding the impact of the campaign on partisan bias vary with assumptions about the nature of partisan bias, the nature and function of discourse about the economy, and the nature of the campaign's impact on voter attention to economic discourse. Alas, the empirical literature offers little reason to form strong expectations on any of these points—a diversity of assumptions are commonly made, with empirical evidence available to support each 1 This view comports with the findings of Duch, Palmer and Anderson (2000), discussed below. 91 view. The approach of the present chapter is, consequently, catholic. This section presents the theoretical possibilities in each area and then considers the empirical implications of each possible combination of assumptions. Partisan Bias Two broad theoretical approaches to the general phenomenon of partisan bias are prominent in the literature. The first view holds that partisanship functions as an information shortcut (per discussion in Chapter One). The basic idea is that, in the absence of information that is directly relevant to the formation of a given perception, voters make inferences from partisanship that substitute for the missing information. The proposition has been established most impressively in the domain of candidate perception (Lodge and Hamill 1986; Conover and Feldman 1989; Rahn 1993). Here, voters have been found to draw on "partisan stereotypes" (Rahn 1993) and schemas (Lodge and Hamill 1986) to 'fill in the blanks' in their perceptions of candidates—for instance, by inferring a candidate's policy positions and other traits from knowledge of the candidate's partisanship. A similar process could be at work in the economic domain. Strong partisans may infer that economic conditions are good when their party is in office, providing they regard their party as a competent economic manager (cf. Kinder and Mebane 1983; Conover, Feldman and Knight 1987). A crucial implication of the shortcuts argument for the present analysis is that reliance on shortcuts decreases as information levels increase. That is, as voters acquire information that is more directly relevant to a given perception—say, a candidate's explicit statement on a policy issue or information concerning real economic conditions—they should be less likely to fall back on partisan stereotypes and schemas 92 (e.g. Lodge and Hamill 1986; Sniderman, Brody and Tetlock 1991). As regards campaign learning in the economic domain, then, if the campaign generates economic information that is directly relevant to the formation of national economic perceptions, partisan bias in such perceptions should fall with the approach of Election Day. A complication with this line of argument concerns the amount of information voters require to make use of shortcuts in the first place. For perceptions of candidate characteristics, the link seems obvious and, therefore, likely to be ubiquitous. This may not be the case for the economy. That is, the link may require knowledge of frames— frames that help voters to make connections between partisanship and national economic perceptions (Mutz 1994, 1998). Put differently, the partisan shortcut may be non-automatic, in the sense described in Chapter One. Results in Duch, Palmer and Anderson (2000) and Bartels (2002) would tend to support this view. The impact of the campaign, then, may not be bias reducing at all. As discussed in Chapters One and Two, of crucial importance here is the nature of campaign discourse concerning the economy, and the relative proportions of framing and raw economic data present in that discourse. More on these distinctions in campaign discourse is presented below. Note for now that, under certain conditions, the impact of the campaign may be to increase reliance on partisan shortcuts in the formation of economic perceptions. The second view of partisan bias is less concerned with inference processes in the absence of information than it is with reception processes in the presence of information. 2 This is the implication of findings in Conover, Feldman and Knight (1987), who find that partisanship and other political attitudes have a greater impact on prospective (i.e. future-oriented) than retrospective (i.e. past-oriented) economic perceptions. This finding is consonant with the 'partisanship-as-shortcut' hypothesis, at least insofar as information relevant to retrospective judgements is intrinsically more accessible than comparable information for prospective judgements. 93 This view focuses on selective attention to and biased perception of incoming information and is, in fact, the classic view of partisan bias in political perception (see, especially, Lazarsfeld, Berelson and Gaudet 1944; Berelson, Lazarsfeld and McPhee 1954; Campbell, Converse, Miller and Stokes 1960, 1966; Finkel 1993; Granberg 1993; Bartels 2002). The argument is that voters filter political information and bend their political perceptions in the direction of partisanship in order to minimize the psychic stress associated with dissonance in one's belief system (Festinger 1957). Applied to the economic domain, the expectation is that voters either ignore or distort economic information that implies perceptions of the national economy that are uncongenial to their partisan inclinations—i.e. good economic news when their party is out, bad economic news when their party is in. The result is systematic bias in economic perceptions according to partisanship. The tendency to filter or distort economic information that is inconsistent with one's partisan commitments should increase as awareness of such inconsistency increases (Festinger 1957), and this awareness, in turn, should be a function of sophistication levels (Sniderman, Brody and Tetlock 1991; Zaller 1992). That is, as one's store of political information increases, especially information that posits links between partisanship and economic perceptions (i.e. framing discourse), the likelihood of selective attention and biased perception should increase. Thus, the impact of the campaign on partisan bias that is rooted in these processes may be to increase partisan bias, depending on, again, the relative proportions of framing cues and raw economic data in campaign discourse. Here, then, the predictions of the 'shortcuts' and 'biased perception' interpretations of partisan bias converge, with complications for the analysis as discussed below. 94 Campaign Economic Discourse As suggested above, predictions about the impact of the campaign on partisan bias in national economic perceptions depend crucially on assumptions about the nature of campaign discourse about the economy. Indeed, different combinations of assumptions about campaign discourse, on the one hand, and the nature of partisan bias, on the other, can imply that the campaign has a bias-reducing effect, a bias-increasing effect, or no effect at all. The two general forms of campaign economic discourse have already been introduced in previous chapters: raw data and framing discourse. Again, raw data is simply 'raw economic information'—information concerning the objective state of the economy, although not necessarily 'objective' information. Framing discourse, on the other hand, is discourse that makes explicit links between economic conditions and the actions of political incumbents. As discussed in Chapter One, such framing discourse might take the form of explicit attributions of credit and blame for economic outcomes to parties and candidates, or it may appear as more general discourse about the importance of 'economic competence' as a consideration in the vote decision. No matter what the particular form, the key feature of such discourse is that, in contrast to raw data, its character is manifestly political. In practice, these two ideal types may be interlaced in campaign discourse. In fact, this kind of 'mixed' discourse may be the dominant mode of economic information dissemination during election campaigns. But it is important to bear the distinction in mind, for each implies a different pattern of campaign dynamics in partisan bias. Specifically, as suggested above, increases in raw data might, if partisanship functions as 95 an information shortcut, offset partisan bias in economic perceptions. Increases in framing discourse, on the other hand, should increase bias in economic judgement, whether partisanship functions as a shortcut or perceptual filter (see below). The Campaign and Voter Attention Assumptions about the impact of the campaign on voter attention are the final area of important theoretical variation pertaining to this analysis. Again, the three pivotal expectations are outlined in Chapter Two: the campaign has no impact on voter attention, leading to roughly equivalent effects across sophistication levels; the campaign increases voter attention in equal amounts across sophistication levels, leading, again, to similar campaign effects across the electorate; and, the campaign increases voter attention primarily among low sophistication voters, leading to maximum campaign effects within this group. Empirical Implications Now that the range of plausible assumptions about the nature of partisan bias, the nature and function of campaign economic discourse, and the nature of the campaign's impact on voter attention have been reviewed, it is possible to consider the empirical implications of the interaction of these assumptions. This interaction is depicted in Table 4.1, which is modelled on Table 3.1. One notable difference between the tables is that here separate predictions are not presented for automatic and non-automatic assumptions about the nature of shortcutting. The contrast, instead, is between the shortcut assumption in general and the 'bias' assumption—i.e. the assumption that partisan effects are rooted in selective attention and perception. First, some general remarks about Table 4.1. The table depicts twelve 96 combinations of theoretical assumptions, but in fact contains only six unique predictions. This is a crucial fact of the analysis, as alluded to in the introduction of this chapter. That is, the present analysis is in some degree indeterminate theoretically—different theoretical assumptions are compatible with the same pattern of results. Cells 3, 4 and 6 contain a common prediction, as do cells 9, 10 and 12, cells 2 and 8, and cells 5 and 11. This is an obvious difficulty for the analysis. That said, the campaign learning argument is compatible with only one combination of theoretical assumptions—those defined by cell 7—and so the findings can be decisive in this regard. Furthermore, the analysis can distinguish somewhat between assumptions about the nature of campaign discourse, as no prediction is common between the 'raw data' cells and the 'framing' and 'mixed' cells. As discussed below, this fact permits the analysis to be quite instructive theoretically. General remarks aside, consider the specific predictions: - Cells 1 and 7 depict the campaign's impact if partisan bias functions as an informational shortcut and campaign economic discourse is strictly constituted by economic raw data. In both cases, initial bias should be maximized among the low sophistication group, as these voters are most lacking in information directly relevant to economic perception. Likewise, in both cases the campaign's effect on partisan bias should be negative—the campaign should reduce reliance on the partisan shortcut in the formation of economic judgements. Where the predictions of these two cells differ is in the relative magnitude of effects across different sophistication levels. If the campaign drives attention increases for all voters or produces no attention increases at all ('General or Nil ' ) , campaign economic discourse should offset bias in roughly equal amounts across sophistication levels 97 (cell 1). If, on the other hand, attention increases are asymmetrical (i.e. increases are concentrated among low sophistication voters), the bias-reducing effect of the campaign should be maximized among low sophistication voters (cell 7). Cell 7, thus, is the 'campaign learning' cell: the campaign erodes partisan bias for all voters, but does so mostly in the low sophistication group, and so narrows the gap across sophistication levels. Learning also takes place under the conditions of cell 1, of course, but pre-existing knowledge inequalities remain. As will now become clear, learning, in this sense, does not take place under any other combination of theoretical assumptions. Cells 2 and 8 depict the campaign's impact if partisan bias results from selective attention and perceptual bias and the campaign generates only economic raw data. Whether attention increases are general, nil, or concentrated among low sophistication voters, the prediction is the same: initial partisan bias is greatest among high sophistication voters and the campaign has no impact on the magnitude of that bias. That the initial bias is greater in the high sophistication group follows from their greater awareness of the implications of economic perceptions for partisan commitments. For a related reason, the effect of the campaign is blunted here; if the campaign produces only economic raw data, there is no reason to expect awareness of the links between partisanship and economic judgement to rise, either among low or high sophistication voters and under any assumption about the campaign's impact on attention. Cells 3 and 9 imagine the campaign's impact if partisan bias is rooted in shortcutting processes and the campaign generates only framing discourse. Under 98 these conditions, bias is, appropriately, magnified for high sophistication voters and increases for all over the course of the campaign. Increases are steeper for low sophistication voters if attention increases are concentrated in this group (cell 9). In one sense, this latter prediction is the 'worst case scenario': bias increases for all, but especially for low sophistication voters. On the other hand, these asymmetrical bias increases should narrow pre-existing gaps in bias, and so have an equalizing effect, if a perverse one. Cells 4 and 10 depict the impact of the campaign if partisan bias is rooted in selective attention and biased perception and the campaign generates only framing discourse. Predictions here are the same as in 3 and 9, respectively. Bias is concentrated among high sophistication voters (they make the strongest initial partisanship-perception links), the campaign increases bias for all, and asymmetrical increases in attention mean that bias increases most for low sophistication voters. Thus, the shortcut and biased perception accounts blend into each other empirically to the extent that shortcutting is not automatic (i.e. depends on framing cues). This point returns in discussion of results and in the conclusion. Cells 5 and 11 contain predictions for campaign effects if partisan bias functions as an informational shortcut and if the campaign produces both raw data and framing discourse. In a sense, these cells sum the effects in cells 1 and 3, on the one hand, and cells 8 and 9, on the other. The result is a null prediction on all counts. If the campaign generates raw data that reduces shortcutting at the same time as it produces framing discourse that facilitates it, the effects might be 99 largely offsetting. As such, these two impacts of the campaign should be confounded in the analysis, irrespective of varying dynamics in attention. For a similar reason, there may be no systematic differences in the initial effects of partisanship, that is, if pre-existing information is also a mixture of raw data and framing cues. A key implication for the empirical analysis is that, as noted in Chapter One, apparently null effects may in fact conceal a good deal of theoretically important action. - The final predictions are in cells 6 and 12, which imagine the impact of the campaign if partisan bias is rooted in biased perception and attention and campaign economic discourse is a mixture of raw data and framing discourse. The cells can be thought of as the sum of cells 2 and 4, on the one hand, and cells 8 and 10, on the other. The result is a campaign that increases bias for all, although initial effects are larger among high sophistication voters, and which may concentrate bias among low sophistication voters if attention increases are maximized among this group. Overall, the predictions in Table 4.1 make several important points. First, theory is clearly divided on the impact of the campaign on partisan bias. A wide range of predictions are produced by varying combinations of equally plausible assumptions. This point is not well appreciated in the literature. Second, almost none of these predictions are compatible with the campaign learning argument as developed in Chapter One. Evaluating the argument on the basis of theory, thus, produces faint hope for the 'enlightenment thesis.' Third, as noted above, similar predictions about campaign dynamics can be derived from a range of theoretical assumptions. The implication is that 100 the analysis of campaign dynamics cannot resolve all of the theoretical questions surrounding the impact of the campaign. That said, a final important point made by Table 4.1 is that a major theoretical fault line in accounts of the campaign's impact on partisan bias is defined by assumptions about the nature of campaign economic discourse. As indicated above, no prediction straddles this fault line. M E T H O D O L O G Y Paralleling the analysis in Chapters Two and Three, the basic analytical approach of the present chapter is to regress, for each election, national economic perceptions on party identification and interactions of party identification with campaign time, while controlling for important socio-demographics.3 Separate estimates are presented for high and low sophistication voters, along with a preliminary estimation pooling observations from both groups. Negative coefficients on the interactive terms imply linear reductions in bias across the campaigns, while positive coefficients indicate linear increases in bias. A l l estimations are OLS. Two equations figure in the analysis. Note that these are reproduced from Chapter Three—a common set of estimations forms the empirical base of both chapters: NEP = f(p0 + Pi UNEMP + ^INCOME + folNCPID + P^NOPID + fcDAY + ZfikSOCDEMk + u), (3.3) NEP = f(p0 + Pi UNEMP + ^INCOME + folNCPID + ^OPID + fcDAY + $6UNEMP*DAY+ frINCOME*DAY + $%INCP1D*DAY + Z$kSOCDEMk + u), (3.4) where A ^ J P = national economic perceptions; INCOME = income scale (0-1); 3 These vary by election as described in Appendix I . 101 UNEMP = unemployed (dummy); DAY = day of campaign; INCPID = incumbent party identification (dummy); NOPID = no party identification4 (dummy); SOCDEMk = a set of socio-demographic variables (see appendix); and, u = random error. As in Chapter Three, equation (3.3) is the static model. The set-up assumes effects do not vary over time; these estimates are presented for their intrinsic interest, although they do not speak directly to the chapter's theoretical concerns. Estimates for Equation (3.4) are key in this regard. This dynamic model of partisan effects on national economic perceptions contains the key interaction of interest—between incumbent party identification and day of campaign—and also controls for campaign dynamics in two other determinants of national economic perceptions by including the interactions UNEMP*DAYand INCOME*DAY, discussed in Chapter Three. National economic perceptions, levels of political sophistication, and socio-demographics are measured as described elsewhere in the dissertation (in Chapter Two, Appendix Four and Appendix Three, respectively). For its part, party identification is measured quite generically across surveys.5 The typical item is some variation on the following: In federal politics, do you usually think of yourself as a Liberal, Conservative, NDP, Bloc Quebecois, or none of these? [CES 2004] In the models, as indicated above, incumbent partisans and those expressing no party identification (or no major party identification, in the British case) are separated from all 4 For the BES 2001 estimation, the variable pools those with no partisanship and those with non-major party identifications. 5 Exact question wordings appear in Appendix I. 102 others—i.e. those identified with some party other than the government party. The set-up is obviously a simplification. But, the incumbent partisans vs. other partisans contrast does go to the heart of arguments about partisan bias: all other things being equal, incumbent partisans should take a more positive view of the economy than everyone else. Non-partisans are isolated to clarify the perceptual contrast between the voters that matter, that is, those who possess live identification with a political party. RESULTS Analysis will proceed in three stages, focusing strictly on the coefficients of theoretical interest in each model: 03 and 0 8 (full model estimates are reported in Appendix II). First, general estimates of both models are presented for each election; these estimations pool observations across sophistication levels. Next, estimates are presented that condition on sophistication—separate coefficients are reported for high and low sophistication respondents. Finally, the conditional estimates are graphed. This last stage is crucial to addressing the central research questions of the chapter: Does the campaign promote political learning and offset pre-existing inequalities in learning? And what theoretical assumptions best fit the data? General Estimates General estimates for the static model are quite sensible (see Table 4.2). Effects are uniformly positive, although of varying magnitudes. The biggest effect is for the U K in 2001, the smallest for the US in 2000. The median effect is a modest 0.073.6 This suggests that the typical difference between incumbent and non-incumbent partisans in national economic perceptions across these elections is of only minor substantive 6 This is the mean of the effects for New Zealand in 2002 and Canada in 1988. 103 consequence, bearing in mind that the national economic perceptions measure ranges from 0 to 1. This seems good news as regards the quality of vote choice. Still, it remains that partisan bias in NEP is ubiquitous across these elections. Furthermore, depending on the dynamics of partisan bias, this 'general' estimate may seriously understate the ultimate impact of partisanship on economic judgement by Election Day. Estimates for the dynamic model are less hopeful as regards the quality of vote choice. First, most of the interactive terms are statistically insignificant and substantively small, suggesting that the campaign has no detectable effect on partisan bias, either positive or negative. Second, those effects that do reach statistical significance are positive—that is, they imply a campaign that increases, rather than offsets, partisan bias in NEP. The elections concerned are New Zealand 2002 and United States 2000. On the other hand, two statistically insignificant effects of substantively significant magnitudes are negative: Canada 2004 and New Zealand 1996. These elections might have witnessed consequential erosion in partisan bias across their campaigns. Overall, then, pooling observations across sophistication levels produces a pattern of results with mixed theoretical implications. The typical campaign would not seem to ameliorate partisan bias to any significant extent. And we can be certain that the campaign exacerbates bias in two cases. Still, there is a hint that the campaign may reduce bias at times. Does conditioning on sophistication level clarify the pattern? Conditional Estimates As with the general estimates, conditional estimates of the static model are quite sensible (see Table 4.3). A l l estimates are positive and all but three are statistically significant. More strikingly, the effects of partisanship are larger among high than low 104 sophistication voters in nine of the ten elections. In six of these nine cases, furthermore, effects for high sophistication voters are at least twice as large as effects in the low sophistication group. This implies that the theoretical image of partisanship as an automatic shortcut to economic judgement is highly questionable. More plausible, it would seem, is the notion that the link between partisanship and national economic perceptions depends on a non-trivial amount of linking or framing information, whether the link functions as a shortcut in the absence of information or as a perceptual screen in the presence of information. Estimates for the dynamic model carry more equivocal and complex implications. Only one of the interactive terms is significant, for high sophistication voters in Canada in 2004, and it implies a strongly negative or bias-reducing effect. That said, eleven other coefficients are substantively large (>0.0010) and, of these, seven are positive—they imply bias-increasing campaigns. Thus, the estimates suggest that, in most elections, the campaign had some effect on partisan bias in national economic perceptions, often a bias-increasing one. The high level of uncertainty attaching to most of the estimates counsels caution in interpreting these results. Still, this uncertainty comes as little surprise: the analysis is bedevilled by small sample sizes in some cases (especially for high sophistication voters in New Zealand) and by a high threat of multicollinearity in almost every case, resulting from the presence of three overlapping interactive terms in the dynamic model. Furthermore, graphing the estimated effects, as in Figure 1, reveals that substantively significant dynamics in partisan bias may have occurred in many of the elections, even if these effects are estimated imprecisely. It seems sensible, then, not to overlook important 105 patterns in the data simply on account of technical limitations. Interpreting the Dynamics The plots in Figure 4.1 are designed to speak to the structure of the predictions contained in Table 4.1. They depict, for each election, the estimated linear impact of campaign time on the magnitude of partisan bias in national economic perceptions by sophistication level. Thus, at a glance, it is possible to see the group in which the initial partisan effect is maximized, the direction of the campaign's effect on partisan bias, and the relative magnitude of the campaign's effect across sophistication levels. A look across the plots draws attention to an important fact: in all elections, initial partisan bias is greatest amongst the most sophisticated. Indeed, in six elections partisan bias is greater for high sophistication voters throughout the campaign. This rules out, in a sense, the automatic shortcut argument, for if partisanship is a shortcut in the absence of information, its use should be greatest among the least informed. The finding also squares with the clear pattern of results for the static model when conditioning on sophistication. The implication is that arguments emphasizing the importance of framing discourse to the link between partisanship and economic judgement are on the right track. One other observation about the overall pattern of effects is pertinent: for all intents and purposes, all of the predicted effects are greater than zero.7 Put another way, in every case, the effects of partisanship are positive and not theoretically perverse. This makes a nice contrast with the results for unemployment status and income, reported in Chapter Three, which indicated that, in some cases, these effects were the opposite of what theory—and common sense—would imply. This suggests, in accordance with 7 An overly strict reading of the plots implies that predicted effects dipped slightly below zero early in the campaign in three cases among low information voters: Canada 1993 and 2000 and US 2000. 106 broader work on the link between the personal and the political (e.g. Sears 1993; Mutz 1998), that partisanship is indeed easier to connect to political perception than personal attitudes and perceptions, such as perceptions of personal economic condition. These observations aside, what do the plots imply for the chapter's major research questions? For one thing, there is little evidence that the campaign generally decreases partisan bias in national economic perceptions. Eleven of the twenty slopes are positive. Most of these shifts, however, are substantively small and none is statistically significant. Only six of the twenty shifts seem to have made a substantive, if still modest, contribution to the magnitude of partisan bias across their respective campaigns (that is, shifts were roughly 0.10). Of these, three shifts are bias-increasing: among low sophistication voters in Canada 2000 and New Zealand 2002, and among high sophistication voters in New Zealand 1999. The three bias-reducing shifts are: among high sophistication voters in Canada 2000 and 2004, and among low sophistication voters in New Zealand 1996. The overall pattern, then, seems perfectly neutral: the campaign's effect is typically insignificant (by statistical and substantive standards) and, even when the campaign does matter, its effect is as likely to be bias-increasing as bias-reducing. The campaign's effect is also as likely to appear among high as among low sophistication voters. The direction of the campaign's effect aside, is there any tendency for the campaign to narrow the gap between sophistication levels? For the most part, the answer to this question is no. And this makes sense in view of the above: most of the time, the campaign's effect on partisan bias is undetectable. Where the campaign's effect is detectable, in two cases the gap—as indicated by the difference in partisan effects 107 between high and low sophistication voters—narrows to a substantively significant extent. In Canada 2004, partisan bias among high sophistication voters drops dramatically over the campaign, but is basically unmoved among low sophistication voters, for whom the bias is weaker to begin with. This approximates campaign-learning expectations, save for the fact that it is high sophistication voters who apparently have the most learning to do. In Canada 2000, by contrast, the sophistication gap narrows in a perverse way, by offsetting bias in the high sophistication group and exacerbating it in the low sophistication group. The finding is striking, recalling that no theoretical account implies opposite effects across sophistication levels; this point returns below. Finally, the gap increases in two cases—in New Zealand 1996 and 1999. In the former, partisan bias drops among low sophistication voters while it remains essentially unmoved in the high sophistication group. In the latter, the pattern is reversed—the gap grows as bias increases among high sophistication voters. These results, thus, leave the campaign learning argument largely in tatters. There is no general tendency for the campaign to reduce partisan bias in national economic perceptions, nor to narrow the gap in the magnitude of bias across sophistication levels. Most of the time, the campaign's effect is modest in the extreme. When the campaign does matter, it is as likely to increase as decrease partisan bias, and to grow as shrink gaps in pre-existing political learning. How do the results square with the theoretical expectations developed in Table 4.1? Most of the elections approximate some combination of the assumptions. At the same time, however, no election fits only one combination of assumptions, a consequence of the high degree of overlap among predictions, discussed above. Five 108 elections nearly fit the essentially null expectations of cells 5 and 11—where partisanship functions as a shortcut in the context of campaign economic discourse that is a mixture of raw data and framing cues. The elections concerned are Canada 1988, 1993 and 1997, United Kingdom 2001, and United States 2000. None of these elections witnessed any significant movement in partisan bias across their campaigns, neither among high nor low sophistication voters. The one divergence between these elections and the predicted effects is in the clear difference in initial effects across sophistication groups—effects in all cases are clearly maximized among high sophistication voters. This may imply that, even if campaign discourse is mixed in content, pre-existing knowledge differences are defined mainly in terms of knowledge of frames. One election, New Zealand 2002, approximates the common expectations across cells 9, 10, and 12—partisan bias is initially greatest among high sophistication voters but increases sharply in the low sophistication group across the campaign period. These results fit a campaign that features, on the one hand, framing discourse, attention increases predominantly among low sophistication voters, and partisan bias rooted in either shortcutting or biased attention and perception, or, on the other hand, mixed campaign economic discourse, attention increases mainly in the low sophistication group, and partisan bias rooted in biased attention and perception. The four remaining elections do not fit any combination of the plausible assumptions. The strangest case is Canada 2000, where, as noted above, bias decreases among high sophistication voters but increases among low sophistication voters. This clearly perverts the campaign learning argument. One theoretical possibility, however, is that the campaign has different effects across sophistication levels. In particular, the 109 campaign may supply low sophistication voters with sufficient motivation and framing cues to make use of shortcuts, at the same time as it motivates high sophistication voters to pay careful attention to raw economic data, which may be more cognitively demanding in any case. As noted in Chapter One, such a view seems compatible with dual process theories of information processing in social psychology (e.g. Petty and Cacioppo 1986). In this way, the campaign actually may facilitate a kind of 'learning' for all, but a different kind of learning for each. Of course, no other campaign fits this pattern. In Canada in 2004, the campaign cut partisan bias among high sophistication voters almost to nothing, but had very little impact at all on low sophistication voters. This may reflect the kind of intensive information processing hinted at above among high sophistication voters. But then, if the campaign had such motivating power for the information rich, why did it have virtually no effect on low sophistication voters? Now consider an election exhibiting the opposite pattern: New Zealand 1996. There, the campaign cut the bias among low sophistication voters, but hardly moved high sophistication voters at all, who took a quite biased view of economic conditions throughout the campaign. If this reflects an increase in intensive information processing among low sophistication voters, the motivating power of the campaign must have been massive. Why, then, was this effect confined to the information poor? The plot thickens with New Zealand 1999, where the campaign increased partisan bias among high sophistication voters but left the low sophistication group virtually untouched. The overall pattern, then, has murky implications for theory. Half the elections approximate a common and theoretically plausible pattern: the campaign supplies a 110 mixture of framing cues and raw economic data with offsetting effects on the magnitude of shortcutting across the electorate. One election approximates a pattern that is common to three combinations of theoretical assumptions: the campaign supplies framing or mixed economic discourse that increases shortcutting or biased attention and perception over the campaign, with effects concentrated among low sophistication voters to whom the campaign supplies extra motivation for political attention. The four remaining elections fit no combination of the plausible assumptions, exhibiting variable combinations of bias increases and reductions at all levels of sophistication. C O N C L U S I O N The results in this chapter make several important points. Most significantly, the campaign learning argument presented in Chapter One fails. There is no general tendency for the campaign to offset partisan bias in national economic perceptions, nor to narrow the gap in perceptual quality across sophistication levels. For the most part, the campaign's effect is nearly undetectable. And, when the campaign does matter, it is as likely to increase as decrease both bias in perception and gaps in the quality of those perceptions across the electorate. As it happens, this finding comes as little surprise, especially in view of the state of theory relating to partisan bias and campaign effects. A careful review of the variety of assumptions current in the literature, and of the implications of these assumptions when considered in combination, offers little reason to expect the campaign to be a 'learning' experience for voters. Minor adjustments in theoretical perspective lead to dramatic differences in empirical expectations. Most theoretically imaginable campaigns either increase partisan bias in economic judgement or have no effect at all. This crucial I l l point is not well understood in the literature on campaign learning. Theory also supplies different microfoundations for the same campaign effects. The major overlap is between the image of partisanship as a shortcut that requires a non-trivial store of framing information, and the view of partisan bias as rooted in biased attention and perception. The one domain in which the two accounts lead to clearly different predicted effects is where campaign information is a mixture of raw economic data and framing cues. The shortcuts interpretation implies that the two kinds of information work against each other, one decreasing bias, the other increasing it; the biased attention and perception interpretation, on the other hand, anticipates only bias increasing campaigns. It is here that the results of the current chapter are theoretically instructive. Five of the ten elections witnessed no significant campaign dynamics in partisan bias. This comports with the shortcut interpretation of partisanship and the assumption that the campaign produces economic discourse that mixes both raw data and framing cues. Behind these apparently null effects may have been increases in the capacity of voters to shortcut, along with simultaneous decreases in their need to do so. The results are also instructive more generally on the nature of partisan bias. Most of the evidence points away from the view of partisanship as strictly an automatic shortcut to economic judgement. Bias is clearly most pronounced among the most informed. This could mean that partisanship is a shortcut that requires framing cues, as suggested above, or that bias is rooted in patterns of attention and cognitive distortion. Either way, it suggests that context matters, either as it makes shortcutting possible or brings dissonant cognitions into awareness. 112 That said, there are some indications that the campaign can produce the kind of substitution of 'real' information for partisan inference implied by the automatic shortcuts account. Bias clearly drops in a few campaigns—indeed, the only campaign effect to register at conventional levels of statistical significance in the conditional estimates is a massive drop in partisan bias among high sophistication voters in Canada in 2004. This seems to suggest that no one cognitive model fits all: different voters engage in different cognitive practices and in different combinations. Part of the pattern may hinge on the dynamics of campaign attention. No simple theory about the campaign's impact on attention works. The campaign's effect—when it has an effect—may occur at high or low levels of political sophistication. Furthermore, the nature of those effects does not vary systematically across sophistication level, although there is a slight tendency to find mainly bias increases among the information poor and bias decreases among the information rich. This may reflect differentiation in the nature of the campaign's effect on attention across sophistication levels, as suggested above: the campaign may motivate the information rich to become cognitive sophisticates, while at the same time raising the information poor from cognitive pauperism to mere cognitive miser-hood. But the pattern in this regard is very weak—the campaign's effect on attention eludes generalization. Different campaigns motivate different voters in different degrees. This contingency makes a larger point about the results: no simplistic, general assumptions about the nature of the campaign's impact on partisan bias will do. This chapter has underlined what are likely the key variables: the nature of partisan bias, the nature of campaign economic discourse, and the dynamics of attention. 113 Table 4.1. Predicted Campaign Effects by Theoretical Assumptions Campaign Economic Discourse Raw Data Framing Mixed Partisan Bias/ Attention Increases Shortcut Bias Shortcut Bias Shortcut Bias General or Ni l (1) Low, Equal, (2) High, Equal, 0 (3) High, Equal, + (4) High, Equal, + (5) Equal, Equal, 0 (6) High, Equal, + Low Soph. Only (7) Low, Low, (8) High, ' Equal, 0 (9) High, Low, + (10) High, Low, + (11) Equal, Equal, 0 (12) High, Low, + Note: Cell entries indicate predicted (i) sophistication level with highest initial effect, (ii) relative magnitude of effects across sophistication levels, and (iii) direction of effect. 114 Table 4.2. INCPID Effects on NEP and the Campaign: General Model Static Model INCPID Dynamic Model INCPID INCPID *DAY N Canada 1988 1993 1997 0.0738 0.0115 0.0377 0.0119 0.0690 0.0167 0.0645 0.0209 0.0256 0.0221 0.0710 0.0406 0.0004 0.0007 0.0005 0.0009 -0.00(11 0.0015 2803 3004 3157 2000 2004 0.0658 0.0184 0.1130 0.0159 0.0799 0.0268 0.1483 0.0353 -0.0007 [" 0.0015. -0.0017 ' 0.0016 3026 3519 New Zealand 1996 1999 2002 United Kingdom 2001 United States 2000 0.1166 0.0181 0.0771 0.0207 0.0725 0.0177 0.2102 0.0066 0.0369 0.0052 0.1498 \ -0.0019 0.0354 0.0016 0.0552 0.0411 0.0297 0.0295 0.2089 0.0145 0.0214 0.0084 0.0014 0.0018 It''''-^B '^*'' 1 0.0025 ! ; 0.0014 0.0001 * i 0.0008 0.0005 0.0002 1328 1180 1485 4602 17382 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. Table 4.3. INCPID Effects on NEP and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication Static Model Dynamic Model Static Model Dynamic Model PID PID PID WAY N PID PID PID WAY N Canada 1988 0.0963 0.0831 • 0.0005 1524 0.0428 0.0433 " -0.0001 1273 0.0154 0.0299 0.0010 0.0163 0.0267 0.0008 1993 0.0697 0.0477 0.0010 1088 0.0223 -0.0074 0:0012 1767 0.0197 0.0394 0.0015 0.0141 0.0277 0 001 1 1997 0.0688 0.0956 -0.0013 1577 0.0689 0.0492 0.0010 1580 0.0219 0.0541 0 0023 0.0256 0.0501 0.0022 2000 0.0756 0.1189 -0.0022 2069 0.0361 -0.0022 0.0020 957 0.0232 0.0302 0 0015 0.0371 0.0626 0.0026 2004 0.1297 0.2060 -0.0040 1132 0.1002 0.1165 -0.0008 2386 0.0285 0.0537 0.0022 0.0187 0.0397 0.0017 New Zealand 1996 0.1922 0.2049 -0.0006 333 0.0882 0.1318 -0.0026 942 0.0393 0.0647 0.(1026 0.0197 0.0371 0.0017 1999 0.1530 0.1088 0.0027 219 0.0623 0.0441 0.0012 952 0.0448 0.0926 0 004h 0.0236 0.0427 0.0020 .•' 2002 0.0833 0.0882 -0.0003 366 0.0719 0.0221 0.0029 1013 0.0256 0.0368 0.0020 0.0229 0.0405 0.00 IS United Kingdom 2001 0.2367 0.2437 -0.0004 2679 0.1722 0.1576 0.0000 1916 0.0089 0.0194 0.0011 0.0107 0.0249 0.0014 United States 2000 0.0661 0.0414 0.0006 3112 0.0174 -0.0135 o.ooox 3609 0.0102 0.0333 0.0007 _ 0.0108 0.0226 0.0005 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at .10 or better. Figure 4.1. Dynamics of Partisan Bias in NEP by Sophistication Level by Election ON 117 CHAPTER FIVE: THE CAMPAIGN DYNAMICS OF ECONOMIC VOTING There is little doubt that perceptions of national economic conditions matter to vote choice (see, inter alia, Key 1968; Kramer 1971; Fiorina 1981; Lewis-Beck 1988, 2006; Lewis-Beck and Stegmaier 2000; but see Wlezien, Franklin and Twiggs 1997; Evans and Anderson 2006). The stylized truth is this: When the economy is strong, incumbents are returned to office, but when the economy sours, voters express their discontent by 'throwing the rascals out.' The impressive ubiquity of such findings is typically interpreted as a triumph for democratic accountability: the electorate rewards good economic performers and punishes bad ones. As suggested in earlier chapters, one crucial premise of this argument is that perceptions of economic conditions are sound—a premise that would seem to have uncertain validity at best. Still, it is unlikely that economic perceptions are entirely—or even largely— devoid of 'real' economic content. The findings of Chapters Three and Four suggest that, although the campaign may at times increase personal and partisan bias in economic judgements, it may also on occasion reduce bias, at least for some voters. And, importantly, there is much variance in economic perceptions that is not explicable in terms of obvious 'internal' forces; the implication is that 'external' sources of national economic perceptions, including changes in real economic conditions, may be crucial. Economic voting, then, may indeed reflect a serious exercise of democratic accountability. Does the campaign facilitate this process? An enlightening and equalizing campaign, as described in Chapter One, should have two important effects in this regard. First, the campaign should increase the impact of perceptions of national 118 economic conditions on vote choice. Second, the campaign should offset pre-existing inequalities in voters' ability to link economic perceptions to vote choice; that is, assuming politically sophisticated voters are better able to make the link absent the informational inducements of the campaign, the effect of the campaign on the economy-vote link should be maximized among low sophistication voters. This should enable the information poor to catch up to the information rich by Election Day. The dominant assumption is certainly that the campaign has such effects (Markus 1988, 1992; Bartels 1992, 2006; Finkel 1993; Gelman and King 1993; Campbell 2000, 2001). As it turns out, however, there are strong reasons to question the conventional wisdom. For one thing, competing accounts of the psychology of economic voting imply different expectations for the impact of the campaign. Varying assumptions about the behaviour of campaigners and the impact of the campaign on voter attention similarly diversify predictions about the campaign's impact on political learning. And the empirical status of the standard view is more dubious than typically understood: most of the evidence is indirect and carries, at best, equivocal implications (see Chapter One). The present chapter executes a direct test of the conventional wisdom and, at this level, the conclusions are fairly clear: there is a weak tendency for the campaign to focus voter attention on perceptions of economic conditions and to reduce gaps across the electorate in the capacity of voters to link economic judgement to the vote. Even so, the campaign is as likely to have no effect at all on the economy-vote link—the modal finding across the elections is no significant dynamics in economic effects. Theoretical implications are more difficult to summarize. Most of the results fit no imaginable combination of the plausible assumptions. That said, elections that approximate 119 theoretical expectations are fairly uniform in their endorsement of the conventional view of economic voting, even as they bring to light new complications for extant accounts of campaign learning. The chapter is organized as follows. First is a review of theoretical issues. Next is discussion of the methodological approach. This is followed by detailed discussion of results and a conclusion. T H E O R E T I C A L C O N T E X T Theory is divided about the impact of the campaign on the magnitude of economic effects on vote choice, although the division is rarely made explicit. The key debate centres around the nature of economic voting, on the one hand, and the nature of campaign economic discourse, on the other. Theoretical expectations also vary, as in earlier chapters, according to assumptions about the campaign's impact on voter attention. This section first outlines the theoretical possibilities in each area and then considers the empirical implications of varying combinations of the possible assumptions. Economic Voting There are two major ways to think about the impact of national economic perceptions on vote choice, each of which is deeply rooted in the literature. The most common approach is to treat the economy as a 'fundamental' consideration in the vote decision. The language of fundamentals is taken from Gelman and King (1993), although the general principle is widely applied (e.g., Key 1968; Kramer 1971; Lewis-Beck 1988). This view of economic Voting holds that national economic perceptions are directly relevant to the voting calculus. The assumption is that a major function of 120 elections is to permit voters to reward and punish governments for their economic performances and, in this way, to facilitate the exercise of democratic accountability. In this view the 'fully informed voter'—one who possesses all the information necessary to form and act on his/her vote intentions in a preference-consistent manner—will, to a significant extent, involve national economic judgements in vote choice. The major alternative view of economic voting leads to quite different expectations about the habits of the fully informed voter. In the 'shortcuts' interpretation of the economy-vote link the use of economic perceptions is not fundamental to vote choice but is, rather, an information-saving device permitting the voter to economize on cognitive effort (per discussion of shortcuts in Chapter One). The basic idea is that in the absence of information directly relevant to the vote decision—say, detailed information on the administrative competence and policy positions of incumbents and challengers— the voter falls back on perceptions of the economy to make a larger inference about the future performance of the incumbent in all areas of governmental activity. For the present chapter, a crucial implication of this view is that as voters acquire political information the impact of economic perceptions on vote intention should decline. More summarily, the fully informed voter will not involve national economic judgements in vote choice to a significant extent. The two understandings of economic voting, thus, lead to opposite expectations about the impact of the campaign on the economy-vote link. In the 'fundamental' view, the effect of the campaign should be to strengthen the link between national economic perceptions and vote choice, at least insofar as the campaign supplies voters with additional information that frames the vote in economic terms (see below). In the 121 'shortcuts' view, by contrast, the informational onslaught of the campaign is more likely to offset the impact of the economy on the vote, as voters acquire political information directly relevant to the vote decision and, consequently, have less reason to default to economic judgements. The clear contrast between the two images of economic voting is upset, however, if one considers the amount of information voters may require in order to employ the economic voting shortcut at all. That is, in accordance with discussion in Chapter One, the economy-vote link may be an 'automatic shortcut' that voters can deploy without significant guidance from political discourse, or it may be a 'non-automatic shortcut,' one which requires a non-trivial amount of framing discourse to be put into practice (cf. Gomez and Wilson 2003). If the latter, the impact of the campaign may be to increase economic effects on the vote, even if economic voting is a shortcut and not a fundamental. Then again, the informational output of the campaign may reduce the need for economic shortcutting even as it facilitates the link, leading to essentially neutral campaign effects. Campaign Economic Discourse Whatever the psychological basis of economic voting, the impact of the campaign on the strength of the economy-vote link is also conditioned by the nature of campaign economic discourse. The crucial dimension of variation, as in earlier chapters, is the extent to which campaign discourse contains significant framing cues that help voters to link economic conditions to political evaluation. In the literature, assumptions in this domain derive from theories of candidate behaviour and, in particular, expectations about how candidates will evaluate the strategic context of campaigning. 122 The dominant assumption is that one candidate or another always has an incentive to emphasize economic considerations in their campaign appeals (Campbell 2001). The logic is simple: In good times, governing parties have a strong incentive to prime economic considerations. In bad times, opposition parties have an equally strong incentive to draw voter attention to the economy. These assumptions certainly animate Gelman and King (1993), and the general claim underlies most previous work on the campaign's impact on economic voting (Markus 1988, 1993; Bartels 1993, 2006; Finkel 1993; Campbell 2000). The expectation, then, is that campaign economic discourse will always contain the framing cues necessary to forge—or, at least, enliven—the link between economic judgement and vote choice in the voter's mind. An alternative view rests on more contingent assumptions about the strategic exigencies of the campaign. The general point is this: one candidate or another may not always have an incentive to emphasize economic considerations in their campaign appeals. One crucial contingency may be the psychological link, especially in the structure of memory, between economic cognitions and other politically relevant cognitions. Johnston, Hagen and Jamieson (2004), for instance, in their analysis of the US Presidential election of 2000, make a compelling case that the Gore campaign gambled that the benefit of raising (largely positive) economic considerations might be offset by the cost of invoking (largely negative) non-economic associations bound up with memories of the Clinton years, especially evaluations of Clinton's character. The incentive to invoke economic appeals, in other words, was offset by the potential costs of simultaneously bringing less favourable cognitions into awareness. And the incentive to prime the economy may be offset for other reasons. If campaign communications are a 123 scarce resource, for instance, time spent discussing the economy necessarily reduces the amount of time available to raise other considerations, some of which may confer greater electoral advantages than the state of the economy. The basic point, then, is that economic considerations may not always be prominent in campaign discourse—that is, campaign economic discourse may not always contain the framing cues necessary to strengthen the economy-vote link. This argument squares with the view of campaigns as, to a great extent, contingent affairs that are not easily predicted in advance (cf. Johnston et al. 1992; Holbrook 1996; Shaw 1999). The Campaign and Voter Attention The final important area of theoretical variation concerns the campaign's impact on voter attention. The important arguments are, again, covered in Chapter Two. Here, as in earlier chapters, the plausible assumptions are three: First, the campaign has no impact on voter attention, leading to roughly equivalent effects across sophistication levels. Second, the campaign increases voter attention in equal amounts across levels of political sophistication, leading, again, to similar campaign effects across sophistication levels. And third, the campaign increases voter attention primarily among low sophistication voters, leading to maximum campaign effects within this group. Empirical Implications The empirical implications of varying combinations of these assumptions are not obvious. Thus, as in earlier chapters, it is worthwhile to treat the theoretical possibilities explicitly. These possibilities are summarized in Table 5.1. As in Tables 3.1 and 4.1, each cell represents a unique combination of theoretical assumptions—assumptions about the nature of economic voting, campaign economic discourse, and the campaign's impact 124 on voter attention. Along with a reference number, cells contain predictions about the sophistication level with the largest initial economic effects on vote choice (i.e. largest economic effect on the first day of the campaign), the relative magnitude of campaign effects across sophistication levels ('Equal,' greater among 'High' sophistication voters, greater among 'Low' sophistication voters), and the direction of the campaign's effect (+, -, 0). First, a general point about Table 5.1 that echoes remarks in earlier chapters: there is significant overlap in terms of predictions across different theoretical assumptions. Across the table's twelve cells there are only seven unique predictions. The biggest overlap concerns cells 2, 8, 6 and 12, all of which contain a common prediction. Also overlapping are the predictions of cells 1 and 4 and cells 7 and 10. The principal complication of the overlap is that it is difficult to adjudicate between the 'fundamental' and 'non-automatic shortcut' theories of economic voting under different assumptions about campaign economic discourse. Importantly, however, no prediction is common across the 'automatic shortcut' cells, on the one hand, and the 'non-automatic shortcut' and 'fundamental' cells, on the other—a distinction that proves theoretically instructive (discussed below). Note also that campaign learning is predicted by a unique set of theoretical assumptions—those of cell 9. Now consider the specific predictions: - Cells 1 and 7 depict the campaign's impact on economic effects in vote choice if economic voting functions as an automatic shortcut in the presence of framing economic discourse. Under these conditions, the initial effect of economic perceptions should be greater among low sophistication voters—who should be 125 most lacking in information directly relevant to the vote decision—and should fall for all as the campaign progresses and political information is acquired. The one difference between the two cells is the sophistication level in which the campaign's effect is maximized. If the campaign drives attention increases for all or, conversely, produces no increases for anyone, then the effect should be similar across sophistication levels. If, by contrast, the campaign increases attention primarily among low sophistication voters, the drop in economic effects should be maximized in this group. Cells 4 and 10, as noted above, overlap cells 1 and 7; that is, the predictions of cell 4 match those of cell 1 and the predictions of cell 7 match those of cell 10. This is so because, if economic voting is an automatic shortcut, the impact of the campaign is the same irrespective of the presence or absence of framing campaign economic discourse. What matters to the magnitude of shortcutting—if shortcutting is automatic—is the quantity of political information in campaign discourse that is directly relevant to the vote decision. It seems plausible that campaigns always produce this kind of information to a significant extent, so this potential variation is not treated in the theoretical analysis. Cells 2 and 8 depict the campaign's impact if economic voting is a non-automatic shortcut and the campaign produces significant framing discourse. Appropriately, the initial impact of the economy is greatest among high sophistication voters— who are most likely to know the appropriate framing links at the outset. As regards the campaign's impact on the magnitude of economic effects, the basic prediction is for the campaign to have no particular effect. As suggested above, if 126 economic voting is a non-automatic shortcut, it seems likely that the positive impact of increases in framing cues on the strength of the economy-vote link will be offset, at least in some degree, by the impact of general increases in political information, which should reduce reliance on the economic shortcut. A plausible implication of this pattern is for essentially null campaign effects. Cells 6 and 12 also imply null effects, although for different reasons. The cells depict the impact of the campaign if economic considerations are 'fundamental' to vote choice and campaign economic discourse lacks framing cues. Here, the campaign does nothing to prime economic considerations and, at the same time, does not offset economic effects—economic perceptions are crucial to the vote decision, so the acquisition of new information should not upset the link. The result is a campaign that has essentially no effect on the economy-vote link. Even so, initial effects are maximized among high sophistication voters— notwithstanding the 'non-impact' of the campaign, these voters are better able to connect the economy and the vote. Cells 3 and 9 also depict the campaign's effect if economic perceptions are 'fundamental' to vote choice, but, in this case, in the presence of a campaign that supplies significant framing cues. Here, initial effects are greater among high sophistication voters and increase for all with the approach of Election Day. The one contrasting prediction across these cells is in terms of the relative magnitude of effects across sophistication levels. Where attention increases are general or nil, as in cell 3, effects should be roughly equal across levels. Where attention increases are concentrated in the low sophistication group, however, the impact of 127 the campaign should be greater among these voters than others, as depicted in cell 9. Cell 9 is also, as noted above, the 'campaign learning cell': the campaign focuses the attention of all voters on economic considerations and also closes gaps in attention across levels of pre-existing political learning. - Finally, cells 5 and 11 imagine the campaign's effect if economic voting is a non-automatic shortcut and the campaign does not supply significant framing cues. In this case, initial economic effects are greatest among high sophistication voters and decrease for all as the campaign progresses and new political information is acquired. Where attention increases are uniform, so should be the campaign's effect (cell 5); where attention increases favour the low sophistication group, the campaign's effect will be asymmetrical (cell 11). Overall, then, Table 5.1 clearly suggests that theory is divided on the likely impact of the campaign on the magnitude of economic voting and on the distribution of economic voting across the electorate. Different assumptions about the nature of economic voting and campaign economic discourse can lead to quite different predictions about the campaign's effect. At the same time, different combinations of assumptions can also lead to similar predictions, confounding theoretical interpretation. Still, a major fault line, as suggested above, exists between the 'automatic shortcut' view and the 'non-automatic shortcut' and 'fundamental' views of economic voting. Thus, the analysis is potentially instructive about this divide. M E T H O D O L O G Y The basic analytical approach is to specify, for each election, a logit model of incumbent vote intention including national economic perceptions and interactions of 128 those perceptions with campaign time, while controlling for important socio-demographics1 and party identification. As in earlier chapters, separate estimates are presented for high and low sophistication voters, together with the results of a general estimation pooling all voters. Two equations figure in the analysis: INCVOTE = f(po + foNEP + foPAY + folNCPID + fitNOPID + T.$kSOCDEMk + u), (5.1) INCVOTE = f(p\, + faNEP + $2DAY + foNEP*DAY + fiJNCPID + fcNOPID + Z$kSOCDEMk + u), (5.2) where INCVOTE = incumbent vote intention; NEP = national economic perceptions; DAY - day of campaign; INC PID = incumbent party identification (dummy); NOPID = no party identification2 (dummy); SOCDEMk = a set of socio-demographic variables (see appendix); and, u = random error. Equation (5.1) is the static model—it assumes that economic effects do not vary significantly over the campaign. The equation functions as an interpretive baseline of sorts, but can not speak to the chapter's theoretical concerns. In this regard, the crucial estimates are those for equation (5.2), the dynamic model. The parameter of interest here is P3. If positive, the parameter indicates increasing economic effects as the campaign progresses; if negative, it suggests that the campaign reduces the impact of economic perceptions. 1 These vary by election as described in Appendix I. 2 For the BES 2001 estimation, the variable pools those with no partisanship and those with non-major party identifications. 129 The measurement of national economic perceptions, party identification, political sophistication, and socio-demographics is described elsewhere (in Chapters Two and Four and Appendices I and III). Vote intention is measured similarly across surveys. The item from the NAES 2000 is typical: Thinking about the general election in November, if you voted today in the general election for president and the candidates were George W. Bush, the Republican; A l Gore, the Democrat; Pat Buchanan of the Reform Party; and Ralph Nader of the Green Party, who would you vote for? [NAES 2000] As indicated above, in the analysis, vote choice is collapsed into a dichotomy between support for the incumbent and support for non-incumbents. This is obviously a simplification. Economic effects are not generally confined to incumbents—and indeed, economic effects on support for non-incumbents are present in the sample of elections examined here (see, for example, Clarke et al. 2004; Johnston, Hagen and Jamieson 2004; Blais et al. 2002). Still, these effects are typically complementary to the effects on incumbent support—that is, these relationships are typically negative. Thus, operationalizing vote choice as a dichotomy, where 1 indicates support for the incumbent and 0 indicates support for non-incumbent parties, is a useful simplifying assumption that does little violence to reality. The operationalization is also true to the pith-and-substance of the economic voting model—reward and punishment of incumbent governments for their economic performances (Key 1968; Fiorina 1981).4 R E S U L T S As in earlier chapters, interpretation of results proceeds in three parts, with the 3 Question wordings in Appendix I. 4 Note that the dependent variable captures vote intention (measured in the pre-campaign, RCS component of each election study), as using reported vote would erase the time variation in political cognition that is at the heart of the present inquiry. 130 focus on the coefficients of theoretical interest: Pi and P3 (full model estimates reported in Appendix II). First, general estimates of the models are presented and discussed. Second, model estimates are presented within sophistication groups. Finally, these 'conditional' estimates are graphed. This last step permits the chapter to speak to the key research questions: Does the campaign promote political learning and offset pre-existing inequalities in learning? And what theoretical assumptions best fit the data? General Estimates Estimates for the static model neatly fit standard expectations. The impact of national economic perceptions on vote choice is uniformly positive and statistically significant. At the same time, there is much variation in the magnitude of economic effects across these elections. Effect, in this sense, means marginal effect for ambivalent voters, that is, the effect of a unit shift in economic evaluations (from worst to best evaluations) for voters who otherwise have an even chance of supporting the incumbent.5 By this standard, the biggest effects are for New Zealand in 1996 and 1999, where a unit shift in economic perceptions meant a 41-point difference in the probability of incumbent support. Economic effects are smallest for Canada 2004—here, a shift from the most negative to the most positive view of national economic conditions increased the probability of an incumbent vote by just 14 points. The median effect is roughly 24 points (which falls between the effect for New Zealand 2002 and US 2000). Estimates for the dynamic model are not so neatly summarized. Most of the 5 That is, they have a baseline probability of supporting the incumbent of .5, i.e. the linear predictor equals zero. Note that this approach results in the maximum possible marginal effects. The virtue of this approach, however, is that it makes comparisons across elections more sensible than, for example, evaluating marginal effects with other variables set to mean values—in such an approach the baseline probability of incumbent support would vary across elections as a consequence of the shape of the logistic curve, not as a result of real variation in economic effects (see Long 1997 for details). 131 NEP*DAY interactions are statistically insignificant by conventional standards, implying that the campaign has no discernible effect on the economy-vote link. Conventional statistical strictures aside, however, six campaigns would seem to have witnessed substantively meaningful movement in economic effects, and interestingly, half of the coefficients concerned are positive and half are negative. The biggest campaign effect is for New Zealand 1999, where the impact of the economy more than doubled over the weeks leading to Election Day. This shift from a marginal effect of 17 points to one of nearly 48 points is, appropriately, statistically significant. The other statistically significant effect is for the United States in 2000, where the campaign cut the impact of the economy by 8 points (roughly a third of its initial impact). Substantively, though not statistically, significant drops in economic effects also appear for New Zealand 2002 (a drop of 22 points) and United Kingdom 2001 (a drop of 8 points). Two other elections, Canada 1988 and 2004, saw apparent growth in economic effects over their campaigns, with increases of roughly 14 points. The overall pattern, then, seems perfectly offsetting: Most effects are statistically insignificant; the two statistically significant effects are in different directions; and, when considering the broader set of substantively important effects, half are positive and half are negative. This pattern of results offers little basis for strong theoretical conclusions, but it does cast the general campaign learning account into significant doubt. Conditional Estimates Parameter estimates for the static model when conditioning on sophistication also appear quite sensible. A l l effects are positive and of substantively important magnitudes, although a handful fall from statistical significance here. Interestingly, in seven of the ten 132 elections, the effect of national economic perceptions on vote choice is greater among high sophistication than among low sophistication voters. Indeed, in two cases economic effects among the information rich are nearly double those among the information poor (Canada 1988 and New Zealand 2002). This suggests that economic voting is not generally an 'automatic shortcut'—the link requires some knowledge of framing cues that the low sophistication group would seem to lack. Results for the dynamic model are more complex. Most of the effects are statistically insignificant, but many nonetheless imply substantively significant campaign effects. And notably, most such effects are positive—they imply that the link between the economy and the vote strengthens in the campaign. Three of these are statistically significant—among low sophistication voters for Canada 1993, and New Zealand 1996 and 1999. Two other estimates approach significance and imply massive increases in the economy's impact over the campaign—among high sophistication voters in New Zealand 1999 and 2002. At the same time, there is also evidence that the campaign can uncouple the connection between economic and political judgement. Economic effects declined to a statistically significant degree among high sophistication voters during New Zealand's campaign 1996, and the estimate for low sophistication voters in New Zealand 2002 implies a similar drop in economic impact. The general pattern, then, is quite mixed. For the most part, the campaign's impact is minor, by statistical or substantive standards. In a few cases, however, the approach of Election Day would seem to have had a striking impact on the magnitude of economic effects. And although these effects are mostly positive, the campaign can also disrupt the economic voting pattern. 133 Interpreting the Dynamics The crucial analysis is in Figure 5.1. The lines depict, by sophistication level, the estimated linear impact of the campaign on the marginal effect of national economic perceptions on vote choice for ambivalent voters (as described above). These plots, thus, speak directly to the predictions of Table 5.1 and permit a clear assessment of the campaign learning argument.6 Note first that in six elections the campaign seems to have had a discernible impact on the magnitude of economic effects, whereas in four elections it would seem to have had no impact at all. The 'no impact' elections are Canada 1997 and 2000, United Kingdom 2001, and United States 2000. Here, economic effects were roughly as large at the end of the campaign as at the beginning across sophistication levels. Elsewhere, the campaign's effect ranged from very large, as among high sophistication voters in New Zealand 1999, to fairly modest, as among high sophistication voters in Canada 1988. This broad pattern makes an important general point: the impact of the campaign is clearly not uniform—it varies by time, place and, as described below, sophistication level. Looking now at estimated effects, ten of the twenty campaign effects—that is, shifts in the impact of national economic perceptions between the first and last campaign day—are substantively important, if not always statistically significant. Half of these are among high sophistication voters and half are found in the low sophistication group. Three of the five shifts among high sophistication voters are positive (Canada 1988 and New Zealand 1999 and 2002) and two are negative (Canada 1993 and New Zealand 6 Note that, in addition to variations in model specification and measurement of variables, comparison of the plots across elections must observe the fact that the scale of the x-axis varies according to campaign length. 134 1996). Likewise, among low sophistication voters, four of the five shifts are positive (Canada 1993 and 2004 and New Zealand 1996 and 1999) and one is negative (New Zealand 2002). The campaign's effect—when it has an effect—is, therefore, generally positive, irrespective of sophistication level. Put differently, the campaign does promote political learning, as defined by the chapter's research questions, although not always and not strictly among low sophistication voters. Does the campaign narrow the gap between high and low sophistication voters in the propensity to rely on economic perceptions in vote choice? Most of the time, it does not: in seven of the ten elections the campaign has no detectable impact on the gap. But, unlike in earlier chapters, the campaign never seems to increase the difference across sophistication groups. Indeed, in three cases the campaign clearly narrows the gap, although sometimes in unexpected ways: the gap narrowed in Canada 1993 and 2004 as low sophistication voters 'caught up' to high sophistication voters, but in New Zealand 1999 the gap narrowed as high sophistication voters 'caught up' to low sophistication ones. Overall, however, the results are hopeful from a campaign learning perspective. Of course, the campaign often has no particular effect on the economy-vote link. But, when the campaign does matter, it is likely to increase the impact of economic considerations on vote choice and to narrow gaps in the propensity of voters with different levels of political sophistication to engage in economic voting. How do the results square with the theoretical expectations outlined in Table 5.1? The flat dynamics estimated for Canada 1997 and 2000, United Kingdom 2001 and United States 2000 fit no combination of assumptions. Economic effects in these 135 elections are static over their campaigns and show no significant asymmetry across sophistication levels. If economic effects were significantly larger among high sophistication voters, the elections would fit the essentially null expectations of cells 2, 6, 8 and 12: the cells imply campaigns that either have offsetting effects on voters who employ economic voting as a non-automatic shortcut, or that have no effect on voters for whom economic considerations are fundamental to vote choice. The homogeneity of economic effects across sophistication levels, however, offers little reason to credit this possibility. One election seems to fit the standard campaign learning expectations of cell 9. In Canada 2004, low sophistication voters iearn a fundamental': economic effects grow among these voters over the course of the campaign and, in so doing, the gap across sophistication levels is narrowed. One complication is the fact that the impact of economic perceptions among high sophistication voters is essentially unmoved by the campaign. This might imply a kind of diminishing returns in the priming of economic considerations: beyond a certain point, the impact of the economy may have no room to grow, perhaps because of the importance to the vote decision of other fundamentals, such as ideology and partisanship. Results for Canada 1993 also approximate the expectations of cell 9, with one key exception: not only do economic effects not grow among high sophistication voters, they may actually shrink over the course of the campaign. The decline among high sophistication voters is far from significance, of course, but it raises again a theoretically important possibility noted in Chapter One: the campaign may increase cognitive heterogeneity across sophistication levels. In particular, the campaign may enable low 136 sophistication voters to attend to economic considerations even as it supplies high sophistication voters with the motivation to move beyond shortcutting and focus on considerations directly relevant to the vote decision—policy positions, evaluations of incumbent competence, candidate characteristics and so forth. The pattern for New Zealand 1996 offers further reason to entertain this view. The campaign produced a statistically significant drop in economic effects among high sophistication voters and a statistically significant increase in economic effects among low sophistication voters. The estimated shifts are substantively large and perfectly inverse: in the high sophistication group the effect dropped from 0.49 to 0.31; correspondingly, in the low sophistication group, the effect jumped from 0.29 to 0.47. An important amendment to the conventional wisdom, then, may be that the campaign's effect can vary across sophistication levels not only in terms of magnitude but also in terms of direction. Two other elections hint at the conventional, 'fundamentalist' view of campaign learning, as captured in cells 3 and 9, with serious qualifications. Canada 1988 witnessed modest growth in economic effects among high sophistication voters, though not by conventional standards of statistical significance. At the same time, however, the campaign saw no movement in the low sophistication group. Perhaps the campaign failed to supply the extra motivation for exposure necessary to overcome chronic low attention to political communications. In any case, if this is campaign learning, it is asymmetrical in nature and more likely to increase than offset pre-existing gaps in political learning. Even more puzzling are results for New Zealand 1999. Here, economic effects increase in both sophistication groups but, again, the dynamics are 137 asymmetrical. The campaign produces a massive increase in economic effects among high sophistication voters, while generating an increase less than half as large in the low sophistication group. More strikingly, initial effects are larger among low than among high sophistication voters—it is the information rich that need to 'catch up' over the campaign, not the information poor. Such a pattern does not comport with any obvious account of the campaign's effect. However, the most theoretically puzzling results by far belong to New Zealand 2002. Here we observe the cognitive heterogeneity pattern as described above, except that the pattern is reversed: economic effects crash over the campaign among low sophistication voters, even as they grow at a tremendous pace among high sophistication voters. Theory is no guide in this case. Any explanation must pervert standard expectations about the causes and consequences of informational differences, and about the campaign's impact on voter attention. Part of the answer may also involve different sophistication groups accessing different discourses. That is, the information rich may sometimes access a discourse that frames economic perceptions, at the same time as the information poor attend to a discourse free of such framing cues, say, a discourse of candidate character traits. Variation in media preferences across sophistication levels may figure in such an account; this possibility is taken up in the conclusion. Still, it bears emphasis that there is no indication of such a high level of informational heterogeneity elsewhere in the data. The overall pattern, then, as in earlier chapters, has ambiguous implications for theory. Just one election fits campaign-learning expectations. Most of the other elections approximate some combination of assumptions, although quite imperfectly. In a couple 138 of cases, the campaign's effect appears quite perverse, raising the possibility of profound heterogeneities in the function of the campaign across sophistication levels. A l l in all, the total pattern casts real doubt on the standard view. C O N C L U S I O N If election campaigns are broadly educative experiences for voters, and if they serve to reduce large, chronic inequalities in the political sophistication of the mass public, then the impact of the typical campaign should be to increase the effect of economic perceptions on vote choice, especially among low sophistication voters. The present chapter uncovers modest evidence for this view. To be sure, in some of the elections examined, the campaign's effect is undetectable. But, when the campaign does have an effect, it is generally to strengthen the link between economic and political judgement. The result is often, though not always, a narrowing of the gap between low and high sophistication voters. And happily, in none of these elections did the campaign appreciably exacerbate pre-existing inequalities in political learning. The theoretical implications of this pattern are more difficult to summarize. Results for five elections comport with no theoretically imaginable campaign. One election fits campaign learning expectations perfectly—the information poor catch up to the information rich as economic effects grow in the former group and remain stable in the latter. Two others approximate the campaign-learning pattern, but with an unexpected wrinkle: a downturn in economic effects in the high sophistication group, even as effects increase for low sophistication voters. Two final elections also echo campaign-learning expectations—economic effects grow over time—although learning is asymmetrically found among high sophistication voters. 139 These diverse results carry equivocal implications, but it seems clear that, for the most part, the campaign's effect—when it has one—is to increase, not decrease, economic effects. This casts some doubt on the image of economic voting as an automatic shortcut for which voters can substitute better information as the campaign proceeds. The fact that economic effects are almost always larger among high than among low sophistication voters makes a similar point. The non-automatic shortcut view also seems doubtful. The interpretation implies a campaign with offsetting or negative effects on the economy-vote link, irrespective of sophistication level. No election produces results that fit with this pattern. The image of economic considerations as fundamental to the vote decision, thus, may be sensible. If the campaign has an effect on economic voting, it seems generally to be to concentrate attention on the economy, never to divert attention from it. But there are important exceptions to this rule: sometimes the campaign focuses the information poor on the economy even as the attention of the information rich is focused elsewhere. As suggested above, the pattern may turn on variation in the campaign's effect on voter cognition across sophistication levels. This argument raises an important possibility: using shortcuts requires sophistication, but it requires even more sophistication not to use them. The impact of the motivational and informational surge of the campaign, thus, depends crucially on the voter's starting point. The curious results for New Zealand 2002, which witnessed increasing economic effects among high sophistication voters and decreasing effects for low sophistication ones, raises the possibility of even deeper heterogeneity in the campaign's effect. Specifically, if the informational context of the vote decision varies not only 140 quantitatively but also qualitatively, expectations across sophistication levels may be dissimilar, cognitive heterogeneity aside. Imagine, for instance, an election in which low sophistication voters watch television news and high sophistication voters read the newspaper. If television news is relatively more candidate-focused and newspapers are relatively more issue-focused, the level of exposure to the kinds of framing cues that facilitate economic voting should vary systematically by sophistication level, leading to precisely the kinds of effects as observed for New Zealand 2002. A l l this is, of course, speculation. The general point, however, is that the impact of the campaign on economic voting is neither as regular nor as readily interpretable as the conventional wisdom suggests. With luck, the chapter has fingered some of the considerations likely to be important in explaining the total pattern. 141 Table 5.1. Predicted Campaign Effects by Theoretical Assumptions Economic Priming Discourse Yes No Economic Voting / Attention Increases Automatic Shortcut Non-automatic Shortcut Funda-mental Automatic Shortcut Non-automatic Shortcut Funda-mental General or Ni l (1) Low, Equal, (2) High, Equal, 0 (3) High, Equal, + (4) Low, Equal, (5) High, Equal, (6) High, Equal, 0 Low Soph. Only (7) Low, Low, (8) High, Equal, 0 (9) High, Low, + (10) Low, Low, (11) High, Low, (12) High, Equal, 0 Note: Cell entries indicate predicted (i) sophistication level with highest initial effect, (ii) relative magnitude of effects across sophistication levels, and (iii) direction of effect. 142 Table 5.2. NEP Effects on the Vote and the Campaign: General Estimates Static Model NEP Dynamic Model NEP NEP*DAY N Canada 1988 1993 1997 2000 2004 New Zealand 1996 2 . 1 0 9 5 0.4188 0 . 7 5 3 8 0.3150 0 . 9 1 5 1 0.1994 0 . 6 4 0 0 0.1574 0 . 5 6 9 2 0.1761 2 . 3 7 0 9 0.3088 1.3213 1.0624 0.6852 0.5203 0 . 9 1 4 9 0.3194 0.5742 0.3751 0.2441 0.3382 2 . 0 6 6 9 0.4298 0.02'" i 0.0127 0.0031 0.0213 0.0000 0 0158 0.0033 0.0150 o . n w i o 0.0155 0.0168 0.0280 2803 3004 3157 3026 3519 1328 1999 2002 2 . 3 3 7 1 0.4052 1 . 0 3 5 8 0.6105 0.7198 0.8437 1 . 6 3 2 4 0.9167 0 . 1 0 3 8 0.0457 -0.0327 0.0662 1180 1485 United Kingdom 2001 2 . 1 3 1 4 0.1970 2 . 5 3 5 2 0.4391 -0.0263 0.0230 4602 United States 2000 1 . 0 1 9 0 0.0691 1 . 2 1 9 0 0.1340 - 0 . 0 0 6 3 0 00^8 17382 Note: Main cell entries are OLS estimates. Robust standard errors below. Coefficients in bold significant at. 10 or better. Table 5.3. NEP Effects on the Vote and the Campaign: Estimates by Sophistication Level High Sophistication Low Sophistication Static Model Dynamic Model Static Model Dynami z Model NEP NEP NEP*DAY N NEP NEP NEP*DAY N Canada 1988 2.7327 1.7055 0.0385 1524 1.1917 0.9959 0.0077 1273 0.5104 1.0511 0.03S3 0.6344 1.6745 0 0492 1993 1.5474 1.9443 -0.0200 1088 0.2922 -0.6438 0.0403 1767 0.5930 1.1238 0.0546 0.3133 0.5399 (10228 1997 1.0698 0.8834 . 0.0095 1550 0.8167 0.7940 0.0012 " 1521 0.3087 0.6313 0.0279 0.2958 0:5600 0 024s 2000 0.6219 0.3757 0.0124 2069 0.6959 0.9699 -0.0139 957 0.2040 0.5842 o ore 0.3509 1.0492 0.0465 2004 0.7762 0.9127 -0.0074 1132 0.4139 -0.0244 : 0.0224 2386 0.2786 0.6073 0 0290 0.2311 0.4416 0.0211 New Zealand M M H 1996 2.9030 4.3989 -0.0794' 328 2.3645 1.3290 „ 0.0567 942 0.6685 1.0419 0 0442 0.3644 0.6106 1999 1.2818 ' -1.1740 0.1846 206 2.5188 1.1023 11.001.* 952 1.4886 2.1233 0 11*7 0.3759 0.6812 0 0394 2002 2.0253 -0.2749 0.1339 362 0.9636 2.7103 -0.0924 1008 0.9267 1.5993 0 0X26 0.7779 1.2007 0 0692 United Kingdom 2001 2.1856 2.7696 -0.0385 , 2679 2.0345 2.0112 " : 0.0015 1916 0.2866 0.6312 ()0<4K 0.2478 0.5108 11.02X0 United States 2000 0.8387 0.6642 0.0046 I - .'11! 3112 0.8431 0.9616 -0.0031 3609 0.1918 0.5224 - 0.0 M 7; ; 0.1445 0.4497 0.0103 Note: Main cell entries are logit coefficients. Robust standard errors below. Coefficients in bold significant at .10 or better. Figure 5.1. The Dynamics of NEP Effects on the Vote by Sophistication Level by Election 4 ^ 145 CHAPTER SIX: CONCLUSION The analysis in this dissertation is motivated by two hypotheses. The first, put simply, is that election campaigns facilitate political learning. That is, the progress of the campaign increases voter knowledge of and attention to the 'fundamental' elements of the vote decision. The second hypothesis is that the progress of the campaign reduces inequalities in political learning. That is, the approach of Election Day narrows the gap between the politically sophisticated and unsophisticated in knowledge of and attention to these 'fundamentals.' Neither hypothesis finds much support here. Indeed, almost every test reported in the foregoing chapters uncovers disconfirming evidence. To rehearse the major findings: - There is no general tendency for the campaign to reduce non-response in measures of national economic perception, nor to equalize rates of non-response across levels of political sophistication. - The campaign does not generally erode personal and partisan biases in economic judgement. In fact, the typical impact of the campaign is neutral. But, when the campaign does matter, it is as likely to magnify as erode bias in national economic perception. Furthermore, the progress of the campaign typically has no significant impact on the relative magnitude of personal and partisan biases across sophistication levels. - Finally, there is a weak tendency for the campaign to increase the impact of national economic perceptions on vote choice and to reduce the gap across levels of political sophistication in terms of voters ability to link economic 146 considerations to the vote. The dissertation also has broader theoretical implications. In particular, much in the foregoing chapters challenges the conventional wisdom concerning the role of 'information shortcuts' in political cognition. Most of the evidence here suggests that the image of shortcuts is either overly simplified or altogether misguided. The standard interpretation suggests that the use of shortcuts to political or economic judgement should decline as information directly relevant to judgement is acquired. For instance, shortcuts to national economic perception should become less useful as real information about national economic conditions—reports of leading economic indicators, for example-becomes more plentiful. The expectation, accordingly, is that the progress of the campaign, and the presumed increase in information that attends it, should reduce reliance on shortcuts. As noted above, this prediction fails empirically. Furthermore, the dissertation underlines multiple theoretical complications with the standard shortcuts view. For one thing, what is often interpreted as 'shortcutting' can equally be interpreted as perceptual bias. For another, even in a shortcutting world, the impact of the campaign depends crucially on the nature of campaign discourse. Different discourses should have different effects on levels of shortcutting, some increasing (framing discourse), some decreasing (raw data) and some neutral (mixed discourse). The negative findings on the question of shortcuts, along with findings concerning differentiation in campaign effects across levels of political sophistication, force related theoretical questions. In particular, they draw attention to the nature of cognitive heterogeneity in political cognition and suggest that the campaign may have different 147 effects on different individuals. One possibility is that highly motivated, political sophisticates process campaign information more intensively, making use of raw data as it becomes available and forming economic and political judgements deliberately. Low motivation, political non-sophisticates, by contrast, may absorb only enough campaign information to facilitate cognitively economical judgement, say, by absorbing framing discourse that facilitates a shortcutting process. In this way, a campaign that informs is also a campaign that divides, by aiding sound, data-based judgement among the information rich, while facilitating cognitively cheap and potentially biased inference processes among the information poor. The dissertation, thus, reveals that the enlightenment and equalization hypotheses are problematic both empirically and theoretically. The impact of the campaign on political learning is more complex and more elusive than the conventional wisdom would suggest. This conclusion opens up a range of new research possibilities—an important subset of these are examined below. First, however, it is important to address the limits of the analysis. LIMITS Impressive though the consistency of the dissertation's results may be, there are important potential objections to the present analysis. This section organizes these objections into two broad categories: technical objections and constraints on theoretical and empirical generalizability. Technical Objections One obvious objection to the analysis is the exclusive focus on the campaign period itself, that is, the fact that the analysis starts when the formal election period starts. 148 As a result, the implicit baseline against which campaign period change in the quality of political cognition is evaluated is effectively the early campaign. One possible consequence of this approach is that the range of political learning may be compressed, assuming significant learning occurs in the run-up to the election period. Campaign dynamics in the quality of political cognition, then, may simply reflect incidental movement around a campaign period mean that is considerably higher than its non-campaign level. Two possible answers to this objection suggest themselves. First, there is much evidence that campaign dynamics are not constrained to merely incidental movement. The occasionally striking dynamics reported in this dissertation obviously make this point, as does the growing record of campaign effects elsewhere (e.g. Johnston et al. 1992; Johnston, Hagen and Jamieson 2004; Ffillygus and Jackman 2003; Fournier et al. 2005). Second, whatever learning may occur in anticipation of the campaign—and, no doubt, learning of a sort does occur (see, e.g. Wlezien and Erikson 2002; Bafumi, Gelman and Park 2004)—pre-campaign learning clearly is not campaign learning. That is, developments in political cognition that precede the arrival of the campaign's distinctive elements—the informational deluge, the mobilization activity, the attractive force of the contest itself—cannot be credited to those elements. Of course, pre-campaign learning is interesting in itself. Even so, that there is apparently no further learning amidst the heightened intensity of the campaign is a fact of some theoretical importance. A more serious objection to the dissertation's analysis concerns modelling approach. Put simply, the search for strictly linear trends may fail to capture important 149 regularities in the campaign's impact on political cognition. The attractive force of the campaign, for instance, may not be fully realized until just before election day—say, within the final week to ten days of the election period (cf. Gelman and King 1993; Campbell 2000). Representing the campaign's effect as a linear trend may, thus, not only misrepresent its functional form but understate the magnitude of its impact. This is an important possibility. Still, any useful interpretation of the enlightenment and equalization arguments surely implies that the campaign's impact is roughly monotonic. For instance, whatever the relationship between campaign time and the impact of economic considerations on vote choice, it must be positive, at least in some degree, over most of the range of the campaign. Such an assumption requires only that those campaign related variables that motivate and inform the voter—the intensity of media coverage and voter mobilization activity, for instance—not decrease over the course of the campaign. Thus, the linear representation should suffice to evaluate the campaign learning argument—the direction of the campaign's impact should be clear, if not its precise form or magnitude. The final important objection to the analysis also concerns the modelling approach. Throughout the dissertation, effects are modelled recursively—that is, independent variables are treated as strictly exogenous to dependent variables. This assumption is potentially problematic for the analyses in Chapters Four and Five. The impact of short-term forces, including economic perceptions, on party identification is the subject of a long and continuing debate (see, especially, Markus and Converse 1979; Fiorina 1981; Franklin and Jackson 1983; Green, Palmquist and Schicker 2002), as lately has become the impact of vote intention on economic perception (Evans and Anderson 150 2006; Lewis-Beck 2006). Furthermore, a recent re-analysis of several pivotal contributions in the campaign effects literature suggests that what may appear as evidence of important dynamics in the weight of various elements in the voting calculus may in fact reflect "vote-driven" campaign learning—i.e. voters reasoning backwards from the vote decision to the various 'determinants' of vote choice (Lenz 2005). No doubt the dissertation's recursive set-ups overstate or understate the impact of the campaign in some cases. Unfortunately, the appropriate correctives are simply unavailable here; that is, plausible instruments for both party identification and national economic perceptions simply cannot be found. For one thing, no important determinant of either variable can plausibly be regarded as exogenous to the relevant dependent variables. For another, only a subset of the election studies (Canada 1993, United Kingdom 2001, and United States 2000) incorporate panel components—to preserve the generality and limit the scope of the analysis, these are not deployed in the dissertation. Nevertheless, the dissertation's major conclusions seem robust to some level of endogeneity between independent and dependent variables. Two arguments make the case. First, it seems clear that the impacts of party identification on national economic perceptions and of national economic perceptions on vote intention eclipse the respective reciprocal effects (see, especially, Green, Palmquist and Schickler 2002 and Lewis-Beck 2006).1 Accordingly, it seems likely that the campaign dynamics estimates are largely a function of over-time variation in the degree of 'forward,' rather than backwards, reasoning between party identification, economic perception and vote intention. Second, in the case of the impact of national economic perceptions on vote intention, the 1 Note that, as regards the vote models in Chapter Five, this is vote intention's effect on national economic perception net of the impact of party identification. 151 possibility that the perception becomes increasingly endogenous to the intention over the campaign in fact introduces a conservative bias as regards the 'no enlightenment' conclusion—that is, it raises the likelihood that the interaction between national economic perceptions and campaign time will be positive. Consequently, the fact that the dissertation uncovers only inconsistent evidence for such a pattern is all the more staking. Even so, the likely presence of reciprocal causation is an ineluctable fact of the analysis, and so the level of uncertainty attaching to the dissertation's conclusions must be correspondingly raised. Constraints on Generalizability One important constraint on the generalizability of the dissertation's results is obvious: the data in the analysis include only ten elections, all of which occurred in Anglo-American democracies within just the past eighteen years. The sample of elections is really one of convenience—these are among the relatively small number of elections for which rolling-cross sectional survey data have been collected. Consequently, the results are potentially unrepresentative of the broader universe of democratic elections. Still, there is much system-level variation across these elections. First, the elections cover four countries and three continents. Second, the elections occurred in political units of widely varying population and size. Third, several basic attributes of the political system and electoral institutions vary across these elections, including regime type, electoral system, party system, the average interval between elections and the length of the campaign period. Finally, key dynamic attributes of the political context vary 2 It bears noting, furthermore, that any impact on economic perception emanating from vote intention is equally upsetting to the enlightenment view. 152 across these data, including government composition, electoral competitiveness and the presence of an incumbent. Thus, at the least, the dissertation's claims are not trapped to a single, peculiar context. Furthermore, the empirical breadth of the analysis is greater than in previous work deploying rolling cross-sectional data, all of which is confined to analysis of dynamics in single elections. The other constraint on the generalizability of the results concerns theoretical rather than empirical breadth; that is, the dissertation's strict focus on the economic domain makes the relevance of the findings for other domains of political cognition unclear. Indeed, the campaign's impact on, for instance, perceptions of candidate policy positions, and on the link between these perceptions and vote choice, may turn out to be quite different. Consequently, broad claims arising out of the dissertation about the nature of campaign learning may be dubious. The status of the enlightenment and equalization hypotheses in other domains is clearly an important topic for future research. That said, there are reasons to suspect results on the economy to be generally diagnostic. Indeed, in some sense, the economy is a 'hard case' for arguments about campaign learning. To a greater degree than, say, perceptions concerning policy positions and, especially, candidate qualities, perceptions about the economy are correctable—through attention to hard economic data, a diversity of expert voices, or even the media. This is not to imply that the objective state of the economy is an obvious, non-contestable or even knowable fact. Rather, it is simply to suggest that the prospects for social—or, at least, expert—consensus concerning economic conditions are better than they are for consensus on a candidate's stand on the environment or level of personal integrity. Consequently, the potential for political 153 learning—defined as the acquisition of objective knowledge about the 'fundamental' variables in the voting calculus—seems inherently greater on economic than on other matters. Thus, if the evidence for campaign enlightenment is thin in the economic domain, it is likely to be at least as thin in other domains. E X T E N S I O N S Notwithstanding the possible limits of the analysis, there is much in the dissertation of theoretical interest. Three extensions to the present analysis immediately suggest themselves. First, claims concerning the broader significance of the present results aside, it remains that the generalizability of the findings beyond the economic domain is an important area for future research. What, for example, is the campaign's impact on perceptions of candidates and parties, in terms of their policy positions, past governing performances, and, in the case of candidates, personal qualities? The enlightenment hypothesis suggests that perceptions should 'improve,' but what this might mean, especially as regards evaluations of past performance and personal qualities, is highly unclear. Enlightenment aside, claims relating to the nature of shortcuts—and to some of the shortcut-sceptic' arguments above—might productively be examined in some of these domains. For instance, a thoroughgoing treatment of dynamics in the impact of party identification across multiple domains would go some distance toward revealing the general impact of the campaign. Second, the analysis might also be extended by picking up on some of the 'technical objections' noted above. First, all of the models in the present dissertation can be readily respecified to incorporate any number of non-linearities in the campaign's 154 impact. Indeed, some of this work has already been completed, with interesting results (Matthews and Johnston 2005). Second, panel measures of variables such as party identification and national economic perceptions might be incorporated, where possible, to offset endogeneity concerns in some of the models. Finally, the analysis might be extended by considering the pre-campaign period. The data base for such an analysis is small but growing—principally the National Annenberg Election Studies of 2000 and 2004. Finally, and perhaps most importantly, future work might take advantage of the comparative breadth of the present analysis. The literature on economic voting strongly suggests that context matters—that certain institutional settings provide better and worse conditions for electoral accountability in the economic domain (Powell and Whitten 1993; Anderson 1995, 2000; Royed, Leyden and Borelli 2000; Nadeau, Niemi and Yoshinaka 2002; Palmer and Whitten 2003). What might this imply for campaign learning? This is a crucial line of inquiry and so merits extended discussion here. Two contextual variables are emphasized in the economic voting literature: clarity of responsibility for political outcomes and the viability of alternatives to the incumbent. Clarity of responsibility probably matters most to the impact of the campaign on the link between economic perception and vote choice, rather than to the nature of economic perception itself. The perception of clear responsibility, in this view, turns largely on objective features of institutional context. Powell and Whitten (1993) argue that economic voting is most likely where government is formed by a single, cohesive party that commands majorities in all legislative chambers, and where oppositional influence through legislative committees is minimized. For campaign learning, high clarity 155 contexts would seem most propitious. If it takes the campaign to connect economic performance to the actions of the incumbent, then it should be easier to make this connection subjectively obvious when the connection itself is objectively clear. In other words, the positive impact of the campaign on the strength of the relationship between national economic perceptions and vote intention should increase with the clarity of responsibility for political outcomes. The viability of alternatives to the incumbent may also be important to campaign learning. The variable refers to the identifiability of a party or set of parties as a plausible alternative government. If voters cannot identify an alternative to the incumbent, according to this logic, then they cannot effectively punish governments for poor economic performance, as there is nowhere else for their votes to go (see, especially, Anderson 2000). This kind of viability obviously has implications for the campaign's impact on economic voting: when alternatives to the incumbent are not viable, it is less likely that the campaign will persuade voters to punish incumbents for economic bad news. At the same time, the presence of a viable alternative to the incumbent seems likely to facilitate other aspects of campaign learning, at least if we make the further assumption that the presence of viable alternatives covaries with the balance of resources across contending campaign organizations. The link here is the competitiveness of the election. Close elections should increase the incentives for resource mobilization among rational party activists and others (Riker and Ordeshook 1971). Insofar as elections with viable alternatives to the incumbent are perforce more competitive than elections where no alternative government is conceivable, high viability elections should also feature a 156 more even distribution of resources across campaigns. If we assume that elections featuring lively competition between equally plausible alternatives are a more enticing draw than elections where there is little uncertainty about the expected winner, then the motivating power of the campaign should increase with the viability of alternatives to the incumbent. And the impact of this motivating power should redound to multiple determinants of economic and political perceptions: non-response should fall, more information should be acquired, and the quality of perceptions might be improved. 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'The Myth of Massive Media Impact Revisited: New Support for a Discredited Idea,' in D. Mutz, P. Sniderman and R. Brody, eds., Political Persuasion and Attitude Change. Ann Arbor: The University of Michigan Press. 166 APPENDIX I: DATA, QUESTION WORDINGS AND MODELING DETAILS Data Sources Data from the 1988 Canadian National Election Study, funded by the Social Sciences and Humanities Research Centre (SSHRC), were collected by the Institute for Social Research (ISR), York University for Richard Johnston, Andre Blais, Henry E. Brady and Jean Crete. Data from the 1993 Canadian Election Study were provided by the ISR. The survey was funded by the SSHRC and was completed for the 1992/93 Canadian Election Team of Johnston, Blais, Brady, Elisabeth Gidengil and Neil Nevitte. Data for the 1997 Canadian Election Study were provided by the ISR. The survey was funded by the SSHRC and was completed for the 1997 Canadian Election Team of Blais, Gidengil, Richard Nadeau and Nevitte. Data from the 2000 Canadian Election Study were collected by the ISR and the Jolicoeur & Associates for Blais, Gidengil, Nadeau and Nevitte. The survey was funded by the SSHRC, Elections Canada and the Institute for Research on Public Policy. The 2004 Canadian Election Study was funded by the SSHRC in partnership with Elections Canada and the Institute for Research on Public Policy. The principal co-investigators of the study were Blais, Gidengil, Nevitte, Joanna Everitt and Patrick Fournier. For the NZES 1996, the principal investigators were Jack Vowles, Peter Aimer, Helena Catt, Raymond Miller, Susan Banducci, Jeffrey Karp, and David Denemark. Funding for the 1996 NZES was provided for by Foundation for Research, Science, and Technology (FRST), the Waikato School of Social Sciences Research Committee and the University of Waikato, University of Auckland Research Committees and Lottery 167 Science. For the NZES 1999, the principal investigators were Vowles, Aimer, Miller, Banducci, Karp, and Ann Sullivan. Funding for the 1999 NZES was provided for by Foundation for Research, Science, and Technology (FRST) and the University of Waikato. For the NZES 2002, the principal investigators were Vowles, Aimer, Miller, Banducci, and Karp. Funding for the 2002 NZES was provided for by Foundation for Research, Science, and Technology (FRST). For the BES 2001, the principal investigators were David Sanders, Paul Whiteley, Harold Clarke and Marianne Stewart. The survey was funded by the Economic and Social Research Council. For the NAES 2000, the principal investigators were Richard Johnston, Kathleen Hall Jamieson and Michael G. Hagen. The NAES was funded by the Annenberg Policy Center. Question Wordings National Economic Perceptions Canada, 1988 Now, I want to ask you about the economy in the COUNTRY as a whole. Would you say that over the PAST Y E A R the economy of the C O U N T R Y has GOTTEN BETTER, S T A Y E D A B O U T THE S A M E OR GOTTEN WORSE? (Would you say M U C H better/worse or SOMEWHAT better/worse?) Canada, 1993 Now, I want to ask you about the economy in all of C A N A D A . Would you say that over the PAST Y E A R the economy of the COUNTRY has GOTTEN BETTER, S T A Y E D A B O U T THE S A M E OR GOTTEN WORSE? (Would you say M U C H better/worse or SOMEWHAT better/worse?) Canada, 1997, 2000, 2004 Now, I want to ask you about the economy. Over the PAST Y E A R , has C A N A D A ' S economy GOTTEN BETTER, GOTTEN WORSE, or S T A Y E D A B O U T THE SAME? 168 New Zealand, 1996 How do you think the general economic situation in New Zealand compares with what it was a year ago? Is it the same, better, or worse? (IF BETTER OR WORSE: A lot or a little?) New Zealand, 1999 How do you think the general economic situation in New Zealand now compares with a year ago? Is it the same, better, or worse? New Zealand, 2002 What do you think of the state of the economy these days in New Zealand? Would you say it is very good, good, bad, very bad, or neither good nor bad? Britain, 2001 How do you think the general economic situation in this country has changed over the last 12 months. Has it got a lot worse, got a little worse, stayed the same, got a little better, or got a lot better? United States, 2000 How would you rate economic conditions in this country today? Would you say they are excellent, good, only fair or poor? Political Sophistication Canada, 1988 1 We would like to know whether you pay much attention to politics G E N E R A L L Y , whether there is an election going on or not. Would you say you follow politics V E R Y C L O S E L Y , F A I R L Y C L O S E L Y , NOT V E R Y C L O S E L Y , OR NOT A T A L L ? How many days IN THE PAST W E E K did you read a daily newspaper? (0-7)' Canada, 1993 (Interviewer rating of respondent's level of political knowledge, as described in text.) 1 The current time orientation of the question raises the possibility that response to the item may be partially endogenous to the campaign. However, regressing the item on day of campaign, reveals only a very modest, positive trend in the item over the campaign: the whole length of the campaign increases reported weekly newspaper reading by just over half a day (results unreported). 169 Canada, 1997 We would like to see how widely known some political figures are. Do you recall the name of the President of the United States? The Minister of Finance of Canada? The Premier/Government Leader of (respondent's province/territory)? The first woman to be Prime Minister of Canada? Canada, 2000 We would like to see how widely known some political figures are. Do you recall the name of the Premier of your province? Do you recall the name of the Minister of Finance of Canada? The Prime Minister of Canada at the time of the Free Trade Agreement with the United States? And do you happen to know the capital of the United States? Canada, 2004 We would like to see how widely known some political figures are. Do you happen to recall the name of the Premier of your province? Do you happen to recall the name of the Minister of Finance of Canada? And the name of the British Prime Minister? The name of the female cabinet minister who ran against Paul Martin for the leadership of the Liberal Party? New Zealand, 1996 (GPI measure as described in Appendix III.) During the election campaign, how often did you follow the election news and political advertising on television, newspapers and the radio, or didn't you follow it at all? (Often, Sometimes, Rarely, Not at all) New Zealand, 1999 (GPI measure as described in Appendix III.) 170 New Zealand, 2002 (GPI measure as described in Appendix III.) During the election campaign, how often did you follow political news, discussions and advertising on television, newspapers and the radio, or didn't you follow it at all? (Often, Sometimes, Rarely, Not at all) United Kingdom, 2001 On a scale from 0 to 10 where 10 means a great deal of attention and 0 means no attention, how much attention do you pay to politics and public affairs? (0-10) United States, 2000 To the best of your knowledge, who favors doubling the amount families can deduct from their income tax for each child they have, George W. Bush or A l Gore? To the best of your knowledge, who favors the biggest increase in spending for Social Security, George W. Bush or A l Gore? On the issue of prescription drugs for senior citizens, to the best of your knowledge, what does George W. Bush think? Does George W. Bush think the federal government should not pay for senior citizens' prescription drugs; the government should offer senior citizens a voucher to cover some of the cost of prescription drugs; or the federal government should cover prescription drugs through Medicare? On the issue of prescription drugs for senior citizens, to the best of your knowledge, what does A l Gore think? Does A l Gore think the federal government should not pay for senior citizens' prescription drugs; the government should offer senior citizens a voucher to cover some of the cost of prescription drugs; or the federal government should cover prescription drugs through Medicare? George W. Bush—do you think he favors or opposes using government funds to make sure that every child in the US is covered by health insurance? To the best of your knowledge, who favors giving a $3000 income tax credit for long-term health care expenses, George W. Bush or A l Gore? A l Gore—do you think he favors requiring a license for a person to buy a handgun? 171 Personal Economic Perceptions Canada, 1988 To help us understand the background to this year's election, we are interested in how people are getting along financially these days. Would you say that you (and your family living there) are BETTER off or WORSE off financially than you were a year ago? (Is that M U C H better/worse off or SOMEWHAT better/worse off?) Canada, 1993 Would you say that you are BETTER off or WORSE off financially than you were a year ago? (Is that M U C H better/worse off or SOMEWHAT better/worse off?) Canada, 1997 Financially, are you BETTER off, WORSE off, or about the same as a year ago? (Is that M U C H better/worse or SOMEWHAT better/worse?) Canada, 2000, 2004 Financially, are you BETTER off, WORSE off, or about the same as a year ago? Britain, 2001 How does the financial situation of your household now compare with what it was 12 months ago? Has it got a lot better, got a little better, stayed the same, got a little worse, or got a lot worse? United States, 2000 How would you rate your own personal economic situation today? Is it excellent, good, only fair or poor? Party Identification Canada, 1988 Thinking of federal politics, do you usually think of yourself as a Liberal, Conservative, NDP or none of these? Canada, 1993, 1997 Thinking of federal politics, do you usually think of yourself as a Liberal, Conservative, NDP, (Reform/Bloc Quebecois) or none of these? 172 Canada, 2000 (Note: Respondents were assigned at random to one of two versions of the party identification question. Responses to these items were combined in the analysis.) Thinking of federal politics, do you usually think of yourself as a Liberal, Bloc Quebecois, Alliance, Conservative, NDP, or none of these? Generally speaking, in federal politics, do you usually think of yourself as a Liberal, Bloc Quebecois, Alliance, Conservative, NDP, or do you usually think of yourself as not having a general preference? Canada, 2004 (Note: Respondents were assigned at random to one of two versions of the party identification question. Responses to these items were combined in the analysis.) In federal politics, do you usually think of yourself as a Liberal, Conservative, NDP, Bloc Quebecois, or none of these? In federal politics, do you usually think of yourself as a Liberal, Conservative, NDP, Bloc Quebecois, another party, or no party? New Zealand, 1996 Generally speaking, do you usually think of yourself as Labour, National, N Z First, Alliance or some other, or don't you think of yourself in this way? New Zealand, 1999 Generally speaking, do you usually think of yourself as Labour, National, NZ First, Alliance, Act or some other, or don't you think of yourself in this way? New Zealand, 2002 Generally speaking, do you usually think of yourself as Labour, National, N Z First, Green, Act or some other, or don't you think of yourself in this way? United Kingdom, 2001 Generally speaking, do you usually think of yourself as Conservative, Labour, Liberal Democrat, (Plaid Cymru/Scottish Nationalist) or what? United States, 2000 Generally speaking, do you usually think of yourself as a Republican, a Democrat, an 173 independent, or something else? Vote Intention Canada, 1988 Which party do you think you will vote for: the Conservative Party, the Liberal Party, the New Democratic Party, or another party? Canada, 1993 If you do vote, which party do you think you will vote for: the Conservative Party, the Liberal Party, the New Democratic Party, the (Reform Party/Bloc Quebecois), or another party? Canada, 1997 Which party do you think you will vote for: the Conservative Party, the Liberal Party, the New Democratic Party, the (Reform Party/Bloc Quebecois), or another party? Canada, 2000 Which party do you think you will vote for? Canada, 2004 Which party do you think you will vote for: the Liberal Party, the Conservative Party, the New Democratic Party, (the Bloc Quebecois,) or another party? New Zealand, 1996, 1999, 2002 Taking the party vote first, if an election were held today, which party would you vote for? United Kingdom, 2001 Which party do you think you are most likely to vote for? United States, 2000 Thinking about the general election in November, if you voted today in the general election for president and the candidates were George W. Bush, the Republican; A l Gore, the Democrat; Pat Buchanan of the Reform Party; and Ralph Nader of the Green Party, who would you vote for? 174 Model Details Note: Sociodemographics; weight. A l l variables are dummy variables unless otherwise indicated. Canada, 1988, 1993, 1997, 2000, 2004: Woman, Age (>55 yrs.=l), Non-European Ethnicity, French Speaker, Catholic, Non-religious, West, Quebec, Atlantic, Degree, Unemployed, Union member/household, Income (scaled 0,1); wt l , cpsnwgtl, cpsnwgtl, cesnwgt, cesnwgt. New Zealand, 1996: Age (scalar), Woman, Homeowner, Working Class Self-Identification, Degree, Union member/household, Public Sector Employee, Unemployed, Income (scaled 0,1); nqwt. New Zealand, 1999: Age (scalar), Woman, Maori, Degree, Union member/household, Public Sector Employee, Manual Worker, Farmer, Unemployed, Income (scaled 0,1); newt. New Zealand, 2002: Age (scalar), Woman, Union member/household, Manual Worker, Unemployed, Income (scaled 0,1); fcamwt. Britain, 2001: Age (scalar), Woman, Homeowner, Southeast, Southwest, Midlands, North, Wales, Scotland, Working Class (objective measure), Unemployed; weight. United States, 2000: Male, Black, Evangelical, Union member/household, Unemployed, Income (scaled 0,1); (no weight). A P P E N D I X II: M O D E L R E S U L T S Table A2.1. Non-Response Models, Canada 1988 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day -0.0069 -0.0024 -0.0037 -0.0087 -0.0043 -0.0056 -0.0037 0.0013 0.0005 (0.0050) (0.0032) (0.0030) (0.0094) (0.0046) (0.0048) (0.0067) (0.0040) (0.0042) Constant -2.7531*** -0.0156 0.2227** -2.9505*** -0.1305 0.0655 -2.6031*** 0.0735 0.3522*** (0.1290) (0.0965) (0.0897) (0.2424) (0.1508) (0.1536) (0.1791) (0.1137) (0.1122) Observations 3582 3582 3582 1859 1859 1859 1711 1711 1711 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 % Table A2.2. Non-Response Models, Canada 1993 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day -0.0032 -0.0028 -0.0029 -0.0090 0.0006 0.0004 -0.0054 -0.0055 -0.0059 (0.0123) (0.0034) (0.0034) (0.0322) (0.0046) (0.0046) (0.0127) (0.0041) (0.0044) Constant -4.0863*** -0.8380*** -0.7608*** -5.1068*** -0.8689*** 0.8406*** -3.6796*** -0.8036*** 0.6912*** (0.3184) (0.0902) (0.0922) (0.7471) (0.1096) (0.1049) (0.3025) (0.1093) (0.1166) Observations 3775 3775 3775 1255 1255 1255 2338 2338 2338 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 Jo Table A2.3. Non-Response Models, Canada 1997 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day 0.0045 -0.0024 -0.0016 -0.0010 -0.0071 -0.0071 0.0082 0.0020 0.0038 (0.0126) (0.0036) (0.0045) (0.0158) (0.0049) (0.0057) (0.0136) (0.0053) (0.0061) Constant -3.2046*** -0.2830*** -0.1258 -3.6581*** -0.2066* -0.1057 -2.9350*** -0.3517*** -0.1484 (0.1865) (0.0913) (0.0990) (0.3448) (0.1160) (0.1362) (0.2229) (0.1358) (0.1312) ' Observations 3949 3949 3949 1886 1886 1886 2063 2063 2063 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 7c Table A2.4. Non-Response Models, Canada 2000 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day 0.0028 0.0046 0.0049 -0.0039 0.0018 0.0014 0.0068 0.0089 0.0103 (0.0099) (0.0035) (0.0035) (0.0153) (0.0045) (0.0044) (0.0159) (0.0070) (0.0068) Constant -3.3768*** -0.4545*** -0.3176*** -3.6476*** -0.5311*** 0.4239*** -2.9363*** -0.2869* -0.0860 (0.2181) (0.0832) (0.0822) (0.3023) (0.1183) (0.1052) (0.3423) (0.1513) (0.1626) Observations 3651 3651 3651 2407 2407 2407 1244 1244 1244 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% ON Table A2.5. Non-Response Models, Canada 2004 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day 0.0180** 0.0023 0.0049 0.0013 -0.0067 -0.0066 0.0227** 0.0059 0.0095** (0.0083) (0.0033) (0.0032) . (0.0146) (0.0050) (0.0051) (0.0110) (0.0043) (0.0043) Constant -3.5948*** -0.1128* -0.0118 -3.4967*** 0.0849 0.2028* -3.6203*** -0.1943** -0.1000 (0.2131) (0.0581) (0.0526) (0.3097) (0.1129) (0.1150) (0.2948) (0.0767) (0.0718) Observations 4323 4323 4323 1342 1342 1342 2975 2975 2975 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 % Table A2.6. Non-Response Models, New Zealand 1996 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day -0.0244* 0.0009 -0.0024 -0.0302 0.0153 0.0115 -0.0286* -0.0027 -0.0067 (0.0131) (0.0048) (0.0051) (0.0244) (0.0123) (0.0120) (0.0148) (0.0052) (0.0057) Constant -2.8947*** -0.5389*** -0.3289*** -3.1011*** -0.9654*** -0.7769** -2.7840*** -0.4396*** -0.2138* (0.3102) (0.1065) (0.1152) (0.4575) (0.3121) (0.3033) (0.3510) (0.1065) (0.1224) Observations 2103 2103 2103 467 467 467 1549 1549 1549 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 Jo Table A2.7. Non-Response Models, New Zealand 1999 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day -0.0012 -0.0019 -0.0020 0.0022 -0.0092 -0.0089 -0.0031 0.0005 -0.0000 (0.0128) (0.0067) (0.0064) (0.0380) (0.0137) (0.0141) (0.0145) (0.0090) (0.0090) Constant -3 2243*** -0.4367*** -0.2787** -3.8539*** -0.3414 -0.2570 -3.1171*** -0.4622*** -0.2866* (0.2484) (0.1275) (0.1274) (0.7657) (0.2821) (0.2890) (0.2739) (0.1670) (0.1704) Observations 1878 1878 1878 369 369 369 1499 1499 1499 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 % Table A2.8. Non-Response Models, New Zealand 2002 General Estimates High Sophistication Estimates Low Sophistication Estimates NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID NEPDK NEPMID NEPDKMID Day -0.0340 0.0033 0.0026 -0.0428 0.0091 0.0082 -0.0528 0.0020 0.0006 (0.0302) (0.0070) (0.0071) (0.0302) (0.0146) (0.0144) (0.0379) (0.0067) (0.0070) Constant -5.0937*** -1.3218*** -1.2883*** -5.2544*** -1.8739*** -1.8360*** -4.6055*** -1 3577*** -1.3058*** (0.7112) (0.1472) (0.1501) (1.0346) (0.3487) (0.3420) (0.9537) (0.1360) (0.1467) Observations 2514 2514 2514 532 532 532 1329 1329 1329 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% -J —i Table A2.9. Non-Response Models, United Kingdom 2001 General Estimates High Sophistication Low Sophistication Estimates Estimates NEPMID NEPMID NEPMID Day 0.0017 0.0048 -0.0021 (0.0023) (0.0048) (0.0051) Constant -1.0048*** -1.1687*** -0.7986*** (0.0492) (0.0991) (0.1060) Observations 4719 2743 1969 Robust standard errors in parentheses * significant at 10 %; ** significant at 5%; *** significant at 1% Table A2.10. Non-Response Models, United States 2000 General Estimates High Sophistication Low Sophistication Estimates Estimates NEPDK NEPDK NEPDK Day 0.0029 0.0150 -0.0100 (0.0047) (0.0340) (0.0086) Constant -5.1285*** r6.9372*** -4.0096*** (0.1697) (1.4080) (0.3155) Observations 19507 3389 4148 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.11. NEP Models, General Estimates, Canada 1988 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.0575*** -0.0548*** -0.0523*** -0.0521*** -0.0522*** -0.0521*** -0.0547*** -0.0545*** -0.0542*** (0.0088) (0.0090) (0.0088) , (0.0088) (0.0088) (0.0088) (0.0090) (0.0090) (0.0090) > 55 yrs. 0.0099 0.0071 0.0211** 0.0209** 0.0211** 0.0209** 0.0070 0.0070 0.0068 (0.0091) (0.0091) (0.0096) (0.0096) (0.0096) (0.0095) (0.0091) (0.0091) (0.0091) Non-European 0.0098 0.0152 0.0171 0.0173 0.0170 0.0172 0.0150 0.0150 0.0148 (0.0169) (0.0172) (0.0160) (0.0160) (0.0160) (0.0161) (0.0172) (0.0172) (0.0172) French Speaker -0.0012 -0.0017 -0.0021 -0.0018 -0.0021 -0.0018 -0.0011 -0.0022 -0.0017 (0.0155) (0.0148) (0.0150) (0.0150) (0.0151) (0.0150) (0.0148) (0.0148) (0.0149) Catholic -0.0051 0.0012 0.0010 0.0008 0.0009 0.0007 0.0005 0.0012 0.0006 (0.0110) (0.0115) (0.0110) (0.0110) (0.0110) (0.0110) (0.0116) (0.0115) (0.0115) Non-religious -0.0003 0.0057 -0.0004 -0.0005 -0.0004 -0.0005 0.0051 0.0055 0.0050 (0.0158) (0.0149) (0.0143) (0.0143) (0.0143) (0.0143) (0.0149) (0.0148) (0.0148) West -0.0144 -0.0174* -0.0133 -0.0133 -0.0133 -0.0133 -0.0173* -0.0176* -0.0175* (0.0100) (0.0101) (0.0102) (0.0102) (0.0102) (0.0102) (0.0101) (0.0102) (0.0102) Quebec 0.0359** 0.0379** 0.0382** 0.0382** 0.0383** 0.0382** 0.0378** 0.0384** 0.0383** (0.0176) (0.0169) (0.0169) (0.0168) (0.0169) (0.0168) (0.0169) (0.0168) (0.0168) Atlantic 0.0084 0.0047 0.0047 0.0047 0.0047 0.0048 0.0049 0.0053 0.0054 (0.0132) (0.0128) (0.0126) (0.0127) (0.0127) (0.0127) (0.0128) (0.0128) (0.0129) Degree 0.0286** 0.0316*** 0.0277** 0.0281** 0.0278** 0.0281** 0.0316*** 0.0307*** 0.0310** (0.0121) (0.0114) (0.0114) (0.0113) (0.0114) (0.0114) (0.0114) (0.0114) (0.0115) Unemployed -0.0244 -0.0227 -0.0073 -0.0076 -0.0070 -0.0074 0.0183 -0.0230 0.0103 (0.0153) (0.0149) (0.0141) (0.0141) (0.0142) (0.0142) (0.0288) (0.0149) (0.0284) Union -0.0305*** -0.0236** -0.0198* -0.0197* -0.0198* -0.0197* -0.0235** -0.0245** -0.0243** (0.0104) (0.0107) (0.0106) (0.0105) (0.0106) (0.0105) (0.0107) (0.0107) (0.0108) Income 0.0659*** 0.0537*** 0.0412** 0.0414** 0.0413** 0.0415** 0.0537*** 0.0093 0.0138 (0.0154) (0.0158) (0.0171) (0.0170) (0.0170) (0.0169) (0.0157) (0.0285) (0.0285) Day 0.0006* 0.0006 0.0005 -0.0004 0.0004 -0.0005 0.0007* -0.0002 -0.0002 (0.0004) (0.0004) (0.0004) (0.0007) (0.0004) (0.0007) (0.0004) (0.0005) (0.0005) PC PID 0.0738*** 0.0642*** 0.0638*** 0.0570*** 0.0592*** 0.0733*** 0.0739*** 0.0645*** (0.0115) (0.0109) .(0.0109) (0.0188) (0.0193) (0.0115) (0.0116) (0.0209) NoPID -0.0043 -0.0060 -0.0061 -0.0060 -0.0061 -0.0042 -0.0047 -0.0047 (0.0112) (0.0112) (0.0111) (0.0112) (0.0112) (0.0112) (0.0110) (0.0111) PEP 0.1348*** (0.0160) 0.0945*** (0.0341) 0.1346*** (0.0159) 0.0953*** (0.0343) PEP*Day 0.0016 0.0016 (0.0011) (0.0011) PC PID*Day 0.0003 0.0002 0.0004 (0.0006) (0.0006) (0.0007) Unemp.*Day -0.0017* -0.0014 (0.0010) (0.0009) —i (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0018 0.0016 (0.0011) (0.0011) Constant 0.5503*** 0.5304*** 0.4607*** 0.4830*** 0.4627*** 0.4838*** 0.5288*** 0.5512*** 0.5504*** (0.0158) (0.0160) (0.0179) (0.0240) (0.0185) (0.0242) (0.0160) (0.0190) (0.0188) Observations 2803 2803 2803 2803 2803 . 2803 2803 2803 2803 R-squared 0.06 0.09 0.11 0.12 0.11 0.12 0.09 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.12. NEP Models, General Estimates, Canada 1993 (1) (2) (3) (4) Woman -0.0497*** -0.0485*** -0.0466*** -0.0466*** (0.0102) (0.0106) (0.0107) (0.0106) > 55 yrs. -0.0367*** -0.0372*** -0.0278** -0.0278** (0.0107) (0.0108) (0.0106) (0.0106) Non-European -0.0030 0.0008 0.0010 0.0012 (0.0163) (0.0163) (0.0163) (0.0163) French Speaker -0.0311 -0.0311 -0.0289 -0.0288 (0.0191) (0.0186) (0.0179) (0.0179) Catholic -0.0299** -0.0257* -0.0250* -0.0250* (0.0132) (0.0139) (0.0139) (0.0139) Non-religious 0.0335** 0.0387** 0.0350** 0.0350** (0.0158) (0.0161) (0.0160) (0.0160) West 0.0083 0.0070 -0.0045 -0.0045 (0.0115) (0.0114) (0.0111) (0.0111) Quebec -0.0089 -0.0083 . -0.0139 -0.0139 (0.0192) (0.0191) (0.0194) (0.0194) Atlantic 0.0254 0.0230 0.0115 0.0117 (0.0187) (0.0184) (0.0185) (0.0185) Degree 0.0091 0.0071 0.0072 0.0073 (0.0119) (0.0121) (0.0125) (0.0125) Unemployed -0.0492** -0.0477** -0.0178 -0.0179 (0.0196) (0.0196) (0.0200) (0.0202) Union -0.0323*** -0.0308*** -0.0265*** -0.0265*** (0.0072) (0.0072) (0.0069) (0.0069) Income 0.0526** 0.0450** 0.0355* 0.0355* (0.0195) (0.0192) (0.0186) (0.0185) Day -0.0003 -0.0003 -0.0002 -0.0003 (0.0004) (0.0004) (0.0004) (0.0009) PC PID 0.0377*** 0.0319** 0.0319** (0.0119) (0.0129) (0.0129) No PID -0.0141 -0.0107 -0.0107 (0.0104) (0.0099) (0.0099) PEP 0.1524*** (0.0187) 0.1479*** (0.0399) PEP*Day 0.0002 (0.0016) PC PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.0467*** -0.0467*** -0.0482*** -0.0484*** -0.0482*** (0.0107) (0.0107) (0.0106) (0.0105) (0.0106) -0.0276** -0.0276** -0.0368*** -0.0366*** -0.0363*** (0.0106) (0.0106) (0.0108) (0.0108) (0.0108) 0.0016 0.0016 0.0007 0.0012 0.0014 (0.0162) (0.0162) (0.0162) (0.0163) (0.0162) -0.0288 -0.0288 -0.0306 -0.0322* -0.0316* (0.0178) (0.0178) (0.0186) (0.0183) (0.0184) -0.0243* -0.0243* -0.0258* -0.0251* -0.0247* (0.0137) (0.0137) (0.0139) (0.0140) (0.0138) 0.0358** 0.0358** 0.0394** 0.0395** 0.0404** (0.0159) (0.0159) (0.0161) (0.0161) (0.0160) -0.0046 -0.0046 0.0072 0.0073 0.0075 (0.0111) (0.0112) (0.0113) (0.0114) (0.0113) -0.0143 -0.0143 -0.0082 -0.0070 -0.0073 (0.0193) (0.0194) (0.0190) (0.0189) (0.0188) 0.0112 0.0113 0.0234 0.0230 0.0231 (0.0185) (0.0185) (0.0182) (0.0183) (0.0182) 0.0072 0.0072 0.0070 0.0076 0.0074 (0.0125) (0.0126) (0.0121) (0.0119) (0.0119) -0.0178 -0.0178 0.0007 -0.0472** -0.0118 (0.0199) (0.0202) (0.0385) (0.0198) (0.0428) -0.0266*** -0.0266*** -0.0305*** -0.0312*** -0.0310*** (0.0069) (0.0069) (0.0072) (0.0073) (0.0073) 0.0350* 0.0350* 0.0447** -0.0366 -0.0309 (0.0184) (0.0183) (0.0190) (0.0417) (0.0439) -0.0004 -0.0005 -0.0001 -0.0017** -0.0016* (0.0005) (0.0009) (0.0004) (0.0008) (0.0009) 0.0111 0.0112 0.0376*** 0.0373*** 0.0256 (0.0246) (0.0246) (0.0118) (0.0117) (0.0221) -0.0108 -0.0108 -0.0144 -0.0132 -0.0136 (0.0099) (0.0099) (0.0104) (0.0103) (0.0103) 0.1525*** 0.1508*** (0.0187) (0.0400) 0.0001 (0.0016) 0.0009 0.0009 0.0005 (0.0010) (0.0010) (0.0009) -0.0021 -0.0015 (0.0013) (0.0015) (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0034** 0.0032** (0.0014) (0.0015) Constant 0.3377*** 0.3318*** 0.2730*** 0.2747*** 0.2773*** 0 2779*** 0.3280*** 0.3641*** 0.3613*** (0.0160) (0.0176) (0.0194) (0.0266) (0.0205) (0.0273) (0.0179) (0.0248) (0.0270) Observations 3004 3004 3004 3004 3004 3004 3004 3004 3004 R-squared 0.06 0.06 0.09 0.09 0.09 0.09 0.06 0.06 0.07 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% OO to Table A2.13. NEP Models, General Estimates, Canada 1997 (1) (2) (3) (4) Woman -0.1100*** -0.1113*** -0.1025*** -0.1026*** (0.0147) (0.0151) (0.0150) (0.0149) > 55 yrs. 0.0181 0.0116 0.0211 0.0211 (0.0175) (0.0169) (0.0170) (0.0169) Non-European -0.0198 -0.0250 -0.0304 -0.0304 (0.0318) (0.0310) (0.0316) (0.0315) French Speaker -0.0818*** -0.0718** -0.0699** -0.0699** (0.0275) (0.0277) (0.0277) (0.0277) Catholic 0.0031 -0.0057 -0.0041 -0.0041 (0.0188) (0.0192) (0.0192) (0.0191) Non-religious 0.0155 0.0153 0.0174 0.0173 (0.0192) (0.0192) (0.0190) (0.0190) West -0.0349** -0.0215 -0.0190 -0.0191 (0.0168) (0.0156) (0.0152) (0.0151) Quebec 0.0005 0.0044 0.0134 0.0134 (0.0281) (0.0278) (0.0280) (0.0281) Atlantic -0.1082*** -0.0988*** -0.0872** -0.0872** (0.0354) (0.0340) (0.0327) (0.0327) Degree 0.0839*** 0.0827*** 0.0803*** 0.0803*** (0.0130) (0.0133) (0.0137) (0.0138) Unemployed -0.1170*** -0.1194*** -0.0801*** -0.0802*** (0.0284) (0.0275) (0.0274) (0.0273) Union -0.0421** -0.0413** -0.0283 -0.0283 (0.0176) (0.0174) (0.0178) (0.0178) Income 0.1633*** 0.1582*** 0.1295*** 0.1295*** (0.0349) (0.0347) (0.0348) (0.0346) Day 0.0002 0.0002 0.0002 0.0002 (0.0008) (0.0007) (0.0007) (0.0012) Liberal PID 0.0690*** 0.0670*** 0.0670*** (0.0167) (0.0162) (0.0162) NoPID -0.0171 -0.0188 -0.0188 (0.0183) (0.0183) (0.0182) PEP 0.2484*** (0.0313) 0.2502*** (0.0635) PEP*Day -0.0001 (0.0029) Lib. PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.1026*** -0.1026*** -0.1113*** -0.1111*** -0.1111*** (0.0149) (0.0148) (0.0151) (0.0150) (0.0149) 0.0210 0.0210 0.0116 0.0116 0.0115 (0.0170) (0.0169) (0.0168) (0.0169) (0.0169) -0.0304 -0.0304 -0.0250 -0.0246 -0.0245 (0.0317) (0.0315) (0.0312) (0.0309) (0.0312) -0.0700** -0.0700** -0.0718** -0.0717** -0.0717** (0.0276) (0.0276) (0.0278) (0.0278) (0.0278) -0.0038 -0.0038 -0.0057 -0.0060 -0.0059 (0.0191) (0.0190) (0.0192) (0.0194) (0.0192) 0.0173 0.0173 0.0153 0.0149 0.0149 • (0.0190) (0.0190) (0.0192) (0.0192) (0.0192) -0.0190 -0.0190 -0.0215 -0.0216 -0.0215 (0.0152) (0.0152) (0.0157) (0.0157) (0.0158) 0.0134 0.0133 0.0044 0.0042 0.0041 (0.0280) (0.0281) (0.0278) (0.0277) (0.0276) -0.0869** -0.0870** -0.0988*** -0.0990*** -0.0988*** (0.0328) (0.0328) (0.0340) (0.0341) (0.0341) 0.0804*** 0.0804*** 0.0827*** 0.0824*** 0.0825*** (0.0137) (0.0138) (0.0133) (0.0133) (0.0133) -0.0802*** -0.0802*** -0.1142 -0.1191*** -0.1168 (0.0274) (0.0272) (0.0694) (0.0275) (0.0694) -0.0283 -0.0283 -0.0413** -0.0413** -0.0413** (0.0178) (0.0178) (0.0173) (0.0174) (0.0173) 0.1296*** 0.1296*** 0.1582*** 0.1418* 0.1418* (0.0347) (0.0345) (0.0347) (0.0728) (0.0728) 0.0002 0.0003 0.0002 -0.0002 -0.0002 (0.0007) (0.0012) (0.0007) (0.0014) (0.0014) 0.0721* 0.0721* 0.0690*** 0.0688*** 0.0710* (0.0393) (0.0392) (0.0167) (0.0165) (0.0406) -0.0188 -0.0188 -0.0171 -0.0170 -0.0170 (0.0183) (0.0182) (0.0183) (0.0183) (0.0184) 0.2484*** 0.2502*** (0.0314) (0.0635) -0.0001 (0.0029) -0.0003 -0.0003 -0.0001 (0.0016) (0.0016) (0.0015) -0.0003 -0.0001 (0.0028) (0.0028) 00 (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0008 (0.0031) 0.0008 (0.0031) Constant 0.5951*** 0.5779*** 0.4564*** 0.4556*** 0.4547*** 0.4539*** 0.5776*** 0.5854*** 0.5845*** (0.0262) (0.0246) (0.0293) (0.0380) (0.0312) (0.0403) (0.0252) (0.0356) (0.0371) Observations 3157 3157 3157 3157 3157 3157 3157 3157 3157 R-squared 0.10 0.11 0.13 0.13 0.13 0.13 0.11 0.11 0.11 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.14. NEP Models, General Estimates, Canada 2000 (1) (2) (3) (4) Woman -0.0840*** -0.0863*** -0.0843*** -0.0843*** (0.0125) (0.0127) (0.0126) (0.0126) > 55 yrs. 0.0499*** 0.0465** 0.0627*** 0.0627*** (0.0172) (0.0176) (0.0172) (0.0172) Non-European 0.0277 0.0241 0.0190 . 0.0190 (0.0233) (0.0231) (0.0216) (0.0217) French Speaker -0.0288 -0.0215 -0.0212 -0.0212 (0.0237) (0.0233) (0.0230) (0.0231) Catholic 0.0189 0.0129 0.0149 0.0149 (0.0210) (0.0211) (0.0209) (0.0209) Non-religious -0.0194 -0.0182 -0.0187 -0.0187 (0.0212) (0.0218) (0.0210) (0.0211) West -0.1276*** -0.1187*** -0.1088*** -0.1088*** (0.0177) (0.0181) (0.0172) (0.0169) Quebec -0.0113 -0.0078 0.0009 0.0009 (0.0199) (0.0199) (0.0200) (0.0199) Atlantic -0.0853*** -0.0814*** -0.0768*** -0.0768*** (0.0233) (0.0231) (0.0213) (0.0212) Degree 0.0728*** 0.0716*** 0.0602** 0.0602** (0.0223) (0.0221) (0.0226) (0.0227) Unemployed -0.0595* -0.0548* -0.0326 -0.0326 (0.0304) (0.0297) (0.0291) (0.0292) Union 0.0033 0.0052 0.0124 0.0124 (0.0143) (0.0144) (0.0137) (0.0137) Income 0.1318*** 0.1254*** 0.1006*** 0.1006*** (0.0226) (0.0226) (0.0206) (0.0206) Day -0.0010 -0.0010 -0.0008 -0.0008 (0.0007) (0.0007) (0.0007) (0.0015) Liberal PID 0.0658*** 0.0502*** 0.0502*** (0.0184) (0.0177) (0.0177) No PID -0.0002 -0.0015 -0.0015 (0.0154) (0.0155) (0.0155) PEP 0.2023*** • (0.0211) 0.2025*** (0.0387) PEP*Day -0.0000 (0.0022) Lib. PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.0844*** -0.0844*** -0.0862*** -0.0863*** -0.0862*** (0.0126) (0.0126) (0.0127) (0.0127) (0.0127) 0.0627*** 0.0627*** 0.0467** 0.0466** 0.0468** (0.0173) (0.0173) (0.0176) (0.0177) (0.0176) 0.0191 0.0191 0.0241 0.0241 0.0242 (0.0215) (0.0216) (0.0231) (0.0231) (0.0231) -0.0217 -0.0218 -0.0215 -0.0216 -0.0221 (0.0228) (0.0229) (0.0233) (0.0233) (0.0233) 0.0149 0.0149 0.0129 0.0129 0.0130 (0.0209) (0.0209) (0.0211) (0.0211) (0.0211) -0.0185 -0.0185 -0.0182 -0.0181 -0.0181 (0.0210) (0.0211) (0.0218) (0.0218) (0.0218) -0.1086*** -0.1086*** -0.1186*** -0.1186*** -0.1184*** (0.0171) (0.0169) (0.0181) (0.0181) (0.0180) 0.0012 0.0012 -0.0078 -0.0077 -0.0074 (0.0198) (0.0198) (0.0199) (0.0202) (0.0201) -0.0769*** -0.0769*** -0.0814*** -0.0813*** -0.0814*** (0.0212) (0.0212) (0.0231) (0.0231) (0.0231) 0.0604** 0.0604** 0.0715*** 0.0716*** 0.0717*** (0.0226) (0.0227) (0.0221) (0.0221) (0.0222) -0.0330 -0.0329 -0.0402 -0.0548* -0.0411 (0.0290) (0.0291) (0.0600) (0.0297) (0.0633) 0.0124 0.0124 0.0052 0.0052 0.0052 (0.0137) (0.0137) (0.0144) (0.0144) (0.0144) 0.1003*** 0.1003*** 0.1255*** 0.1181*** 0.1176*** (0.0206) (0.0206) (0.0226) (0.0387) (0.0400) -0.0005 -0.0006 -0.0010 -0.0012 -0.0009 (0.0007) (0.0015) (0.0007) (0.0010) (0.0011) 0.0657** 0.0659** 0.0658*** 0.0658*** 0.0799*** (0.0265) (0.0273) (0.0184) (0.0184) (0.0268) -0.0016 -0.0015 -0.0000 -0.0001 -0.0001 (0.0155) (0.0155) (0.0154) (0.0155) (0.0155) 0.2023*** 0.1997*** (0.0211) (0.0393) 0.0001 (0.0022) -0.0008 -0.0008 -0.0007 (0.0014) (0.0014) (0.0015) -0.0007 -0.0007 (0.0028) (0.0031) 00 (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0004 0.0004 (0.0016) (0.0017) Constant 0.6581*** 0.6395*** 0.5319*** 0.5318*** 0.5273*** 0.5286*** 0.6387*** 0.6429*** 0.6382*** (0.0257) (0.0293) ' (0.0289) (0.0342) (0.0297) (0.0339) (0.0290) (0.0308) (0.0324) Observations 3026 3026 3026 3026 3026 3026 3026 3026 3026 R-squared 0.08 0.09 0.13 0.13 0.13 0.13 0.09 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% OO Os Table A2.15. NEP Models, General Estimates, Canada 2004 (1) (2) (3) (4) (5) (6) (7) (8) . (9) Woman -0.0977*** -0.0980*** -0.0974*** -0.0973*** -0.0975*** -0.0974*** -0.0994*** -0.0982*** -0.0997*** (0.0148) (0.0144) (0.0137) (0.0137) (0.0136) (0.0136) (0.0145) (0.0143) (0.0143) > 55 yrs. 0.0373** 0.0269* 0.0403** 0.0402** 0.0396** 0.0395** 0.0271* 0.0257 0.0254 (0.0155) (0.0152) (0.0153) (0.0153) (0.0151) (0.0152) (0.0150) (0.0154) (0.0151) Non-European 0.0442 0.0271 0.0203 0.0202 0.0204 0.0203 0.0303 0.0267 0.0300 (0.0318) (0.0324) (0.0329) (0.0330) (0.0328) (0.0329) (0.0314) (0.0326) (0.0315) French Speaker -0.0174 0.0049 -0.0039 -0.0036 -0.0046 -0.0043 0.0057 0.0060 0.0060 (0.0286) (0.0277) (0.0256) (0.0254) (0.0259) (0.0257) (0.0277) (0.0277) (0.0280) Catholic 0.0163 0.0055 0.0061 0.0062 0.0062 0.0063 0.0071 0.0055 0.0071 (0.0137) (0.0137) (0.0139) (0.0139) (0.0139) (0.0139) (0.0136) (0.0138) (0.0136) Non-religious 0.0129 0.0158 0.0081 0.0085 0.0071 0.0076 0.0166 0.0155 0.0153 (0.0203) (0.0205) (0.0200) (0.0200) (0.0201) (0.0201) (0.0202) (0.0207) (0.0205) West -0.0017 0.0107 0.0033 0.0033 0.0039 0.0039 0.0112 0.0104 0.0116 (0.0162) (0.0159) (0.0151) (0.0152) (0.0151) (0.0152) (0.0158) (0.0158) (0.0158) Quebec -0.0059 -0.0154 -0.0125 -0.0127 -0.0115 -0.0116 -0.0157 -0.0168 -0.0159 • (0.0270) (0.0264) (0.0242) (0.0242) (0.0245) (0.0245) (0.0267) (0.0268) (0.0274) Atlantic -0.0132 -0.0129 -0.0230 -0.0228 -0.0235 -0.0233 -0.0124 -0.0130 -0.0129 (0.0238) (0.0228) (0.0221) (0.0221) (0.0219) (0.0219) (0.0229) .(0.0226) (0.0226) Degree 0.0755*** 0.0761*** 0.0665*** 0.0663*** 0.0666*** 0.0664*** 0.0759*** 0.0759*** 0.0758*** (0.0156) (0.0159) (0.0158) (0.0158) (0.0157) (0.0157) (0.0158) (0.0160) (0.0157) Unemployed -0.0849*** -0.0762** -0.0555* -0.0566* -0.0541* -0.0554* 0.0840 -0.0776** 0.0752 (0.0307) (0.0309) (0.0317) (0.0314) (0.0318) (0.0315) (0.0515) (0.0308) (0.0514) Union -0.0116 -0.0107 -0.0121 -0.0121 -0.0119 -0.0119 -0.0108 -0.0110 -0.0108 (0.0175) (0.0173) (0.0172) (0.0172) (0.0173) (0.0172) (0.0173) (0.0174) (0.0174) Income 0.1292*** 0.1192*** 0.1023*** 0.1024*** 0.1024*** 0.1026*** 0.1196*** 0.0539* 0.0613* (0.0167) (0.0166) (0.0169) (0.0170) (0.0167) (0.0169) (0.0170) (0.0319) (0.0315) Day 0.0029*** 0.0030*** 0.0027*** 0.0020 0.0032*** 0.0025* 0.0033*** 0.0014 0.0024** (0.0008) (0.0008) (0.0008) (0.0014) (0.0010) (0.0014) (0.0008) (0.0010) (0.0010) Liberal PID 0.1130*** 0.0969*** 0.0968*** 0.1322*** 0.1347*** 0.1138*** 0.1129*** 0.1483*** (0.0159) (0.0157) (0.0157) (0.0341) (0.0359) (0.0160) (0.0157) (0.0353) NoPID -0.0055 -0.0034 -0.0033 -0.0032 -0.0030 -0.0052 -0.0053 -0.0048 (0.0129) (0.0128) (0.0128) (0.0128) (0.0128) (0.0128) (0.0129) (0.0128) PEP 0.1803*** (0.0207) 0.1530*** (0.0545) 0.1807*** (0.0207) 0.1475** (0.0570) PEP*Day 0.0014 (0.0022) 0.0017 (0.0023) Lib. PID*Day -0.0018 (0.0015) -0.0019 (0.0016) -0.0017 (0.0016) Unemp.*Day -0.0088** -0.0083** (0.0035) (0.0034) 00 — 1 (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0033** 0.0030* (0.0015) (0.0016) Constant 0.3904*** 0.3619*** 0.2997*** 0.3120*** 0.2884*** 0.3025*** 0.3544*** 0.3938*** 0.3724*** (0.0295) "(0.0309) (0.0337) (0.0443) (0.0350) (0.0436) (0.0304) (0.0354) (0.0350) Observations 3519 3519 3519 3519 3519 3519 3519 3519 3519 R-squared 0.07 0.09 0.12 0.12 0.12 0.12 0.10 0.09 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.16. NEP Models, General Estimates, New Zealand 1996 (1) (2) (3) (4) (5) (6) Woman -0.0460*** -0.0450*** -0.0454*** -0.0462*** -0.0456*** -0.0470*** (0.0147) (0.0140) (0.0139) (0.0140) (0.0139) (0.0139) Age -0.0029*** -0.0029*** -0.0029*** -0.0029*** -0.0029*** -0.0029*** (0.0006) (0.0006) (0.0006) (0.0006) (0.0006) (0.0006) Homeowner -0.0043 -0.0112 -0.0113 -0.0119 -0.0108 -0.0114 (0.0231) (0.0224) (0.0226) (0.0222) (0.0224) (0.0224) Working Class -0.0521** -0.0355 ' -0.0353 -0.0362 -0.0367 -0.0372 (0.0239) (0.0229) (0.0230) (0.0229) (0.0229) (0.0229) Degree 0.0158 0.0143 0.0151 0.0147 0.0144 0.0156 (0.0227) (0.0219) (0.0218) (0.0220) (0.0220) (0.0220) Union -0.0259 -0.0163 -0.0175 -0.0149 -0.0148 -0.0150 (0.0197) (0.0191) (0.0193) (0.0188) (0.0191) (0.0190) Public Sector Employee 0.0270 0.0336** 0.0337** 0.0329* 0.0327* 0.0322* (0.0172) (0.0164) (0.0165) (0.0165) (0.0166) (0.0168) Unemployed -0.0148 -0.0017 -0.0027 0.1875* 0.0018 0.1699* (0.0590) (0.0627) (0.0618) (0.0938) (0.0621) (0.0921) Income 0.1077*** 0.0972** 0.0977** • 0.0983** 0.0051 0.0052 (0.0367) (0.0360) (0.0361) (0.0364) (0.0578) (0.0599) Day 0.0027*** 0.0029*** 0.0034*** 0.0031*** -0.0008 -0.0002 (0.0006) (0.0006) (0.0006) (0.0007) (0.0019) (0.0017) National PID 0.1166*** 0.1448*** 0.1169*** 0.1157*** 0.1498*** (0.0181) (0.0337) (0.0180) (0.0181) (0.0354) No PID 0.0159 0.0154 0.0158 0.0142 0.0136 (0.0168) (0.0169) (0.0168) (0.0169) (0.0172) National PID* Day -0.0016 (0.0015) -0.0019 (0.0016) Unemployed*Day -0.0077* (0.0039) -0.0069* (0.0038) Income*Day 0.0049** (0.0024) 0.0050* (0.0026) Constant 0.5286*** 0.4932*** 0.4857*** 0.4904*** 0.5648*** 0.5542*** (0.0326) (0.0326) (0.0311) (0.0323) (0.0487) (0.0459) Observations 1335 1328 1328 1328 1328 1328 R-squared 0.08 0.11 0.11 0.12 • 0.12 0.12 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% OO Table A2.17. NEP Models, General Estimates, New Zealand 1999 (1) (2) (3) (4) (5) (6) Woman -0.0303** -0.0323*** -0.0326*** -0.0320*** -0.0319*** -0.0318*** (0.0114) (0.0107) (0.0107) (0.0108) (0.0107) (0.0108) Age -0.0020*** -0.0021*** -0.0021*** -0.0021*** -0.0021*** -0.0021*** (0.0005) (0.0005) (0.0005) (0.0005) (0.0005) (0.0005) Maori -0.0712* -0.0593 -0.0598 -0.0590 -0.0583 -0.0582 (0.0416) (0.0400) (0.0396) (0.0402) (0.0399) (0.0397) Degree -0.0032 -0.0014 -0.0014 -0.0003 -0.0026 -0.0016 (0.0189) (0.0183) (0.0183) (0.0186) (0.0186) (0.0189) Union 0.0020 0.0103 0.0101 0.0111 0.0109 0.0118 (0.0180) (0.0185) ' (0.0184) (0.0182) (0.0184) (0.0180) Public Sector Employee -0.0202* -0.0183 -0.0181 -0.0196* -0.0190* -0.0204* (0.0107) (0.0110) (0.0110) (0.0111) (0.0108) (0.0109) Manual Worker -0.0287 -0.0234 -0.0235 -0.0236 -0.0244 -0.0249 (0.0262) (0.0261) (0.0262) (0.0260) (0.0256) (0.0255) Farmer 0.0465 0.0284 0.0285 0.0283 0.0279 0.0278 (0.0348) (0.0356) (0.0355) (0.0356) (0.0356) (0.0354) Unemployed 0.0107 0.0171 0.0167 0.0735 0.0167 0.0790 (0.0257) (0.0265) (0.0266) (0.0486) (0.0264) (0.0495) Income 0.1546*** 0.1323*** 0.1315*** 0.1319*** 0.1783*** 0.1874*** (0.0325) (0.0322) (0.0322) (0.0321) (0.0524) (0.0551) Day 0.0026*** 0.0026*** 0.0023** 0.0027*** 0.0042** 0.0043** (0.0009) (0.0008) (0.0009) (0.0008) (0.0017) (0.0018) National PID 0.0771*** 0.0596 0.0770*** 0.0772*** 0.0552 (0.0207) (0.0401) (0.0207) (0.0207) (0.0411) No PID 0.0154 0.0157 0.0148 0.0148 0.0145 (0.0145) (0.0145) (0.0147) (0.0147) (0.0149) National PID*Day 0.0011 (0.0018) 0.0014 (0.0018) Unemployed*Day -0.0033 (0.0026) -0.0036 (0.0026) Income*Day -0.0028 (0.0021) -0.0035 (0.0022) Constant 0.4620*** 0.4458*** 0.4515*** 0 4442*** 0.4208*** 0.4203*** (0.0389) (0.0354) (0.0348) (0.0354) (0.0453) (0.0456) Observations 1180 1180 1180 1180 1180 1180 R-squared 0.08 0.10 0.10 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O Table A2.18. NEP Models, General Estimates, New Zealand 2002 (1) (2) (3) (4) (5) (6) Age 0.0021*** 0.0019*** 0.0019*** 0.0019*** 0.0019*** 0.0019*** (0.0005) (0.0005) (0.0005) (0.0005) (0.0005) (0.0005) Woman -0.0258* -0.0267* -0.0281** -0.0266* -0.0287** -0.0296** (0.0135) (0.0134) (0.0132) (0.0134) (0.0133) (0.0132) Manual Worker -0.0415 -0.0395 -0.0402 -0.0395 -0.0362 -0.0372 (0.0353) (0.0353) (0.0348) (0.0353) (0.0343) (0.0340) Union 0.0214 0.0096 0.0084 0.0095 0.0102 0.0091 (0.0143) (0.0148) (0.0146) (0.0148) (0.0145) (0.0144) Unemployed 0.0183 0.0077 0.0108 -0.0186 0.0116 0.0050 (0.0342) (0.0329) (0.0350) (0.0553) (0.0325) (0.0551) Income 0.0077 0.0184 0.0192 0.0183 0.0926 0.0849. (0.0324) (0.0326) (0.0326) (0.0326) (0.0602) (0.0631) Day -0.0014** -0.0013* -0.0021** -0.0013* 0.0010 -0.0000 (0.0007) (0.0006) (0.0009) (0.0007) (0.0012) (0.0015) Labour PID 0.0725*** 0.0252 0.0726*** 0.0724*** • 0.0297 (0.0177) (0.0295) (0.0177) (0.0174) (0.0295) No PID 0.0102 0.0108 • 0.0101 0.0102 0.0107 . (0.0192) (0.0191) (0.0192) (0.0191) (0.0191) Labour PID*Day 0.0028* (0.0014) 0.0025* (0.0014) Unemployed*Day 0.0017 (0.0035) 0.0006 (0.0034) Income*Day -0.0043 (0.0026) -0.0038 (0.0027) Constant 0.5938*** 0.5719*** 0.5863*** 0.5723*** 0.5340*** 0.5514*** (0.0369) (0.0430) (0.0441) (0.0431) (0.0521) (0.0547) Observations 1485 1485 1485 1485 1485 1485 R-squared 0.04 0.06 0.07 0.06 0.07 0.07 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.19. NEP Models, General Estimates, United Kingdom 2001 (1) (2) (3) (4) (5) (6) (7) (8). Age 0.0007*** 0.0008*** 0.0008*** 0.0008*** 0.0008*** 0.0008*** 0.0008*** 0.0008*** (0.0002) (0.0002) (0.0002) (0.0002) (0.0002) (0.0002) (0.0002) (0.0002) Woman -0.0308*** -0.0257*** -0.0263*** -0.0264*** -0.0263*** -0.0264*** -0.0257*** -0.0257*** (0.0078) (0.0075) (0.0068) (0.0068) (0.0068) (0.0068) (0.0075) (0.0075) Homeowner -0.0439*** -0.0199** -0.0155* -0.0154* -0.0155* -0.0154* -0.0199** -0.0199** (0.0088) (0.0087) (0.0082) (0.0082) (0.0082) (0.0082) (0.0087) (0.0087) Southeast 0.0011 0.0196 0.0188* 0.0192* 0.0190* 0.0192* 0.0198 0.0198 (0.0154) (0.0129) (0.0109) (0.0109) (0.0109) (0.0109) (0.0130) (0.0130) Southwest -0.0271 -0.0042 -0.0030. -0.0023 -0.0029 -0.0023 -0.0040 -0.0040 (0.0201) (0.0179) (0.0165) (0.0165) (0.0164) (0.0165) (0.0179) (0.0179) Midlands -0.0025 -0.0062 -0.0041 -0.0034 -0.0039 -0.0033 -0.0064 -0.0063 (0.0141) (0.0119) (0.0106) (0.0105) (0.0104) (0.0104) (0.0119) (0.0118) North 0.0132 -0.0024 -0.0017 -0.0013 -0.0016 -0.0012 -0.0020 -0.0019 (0.0144) (0.0128) (0.0118) (0.0117) (0.0118) (0.0117) (0.0131) (0.0131) Wales -0.0124 -0.0124 -0.0118 -0.0111 -0.0116 -0.0111 -0.0123 -0.0123 (0.0231) (0.0204) (0.0190) (0.0188) (0.0189) (0.0188) (0.0204) (0.0204) Scotland 0.0007 0.0022 0.0009 0.0014 0.0011 0.0015 0.0020 0.0020 (0.0179) (0.0182) (0.0157) (0.0156) (0.0157) (0.0157) (0.0181) (0.0181) Working Class 0.0179* 0.0009 0.0050 0.0049 0.0050 0.0049 0.0008 0.0008 (0.0095) (0.0089) (0.0087) (0.0087) (0.0087) (0.0087) (0.0089) (0.0089) Unemployed -0.0586** -0.0649*** -0.0497** -0.0499** -0.0495** -0.0499** -0.0941** -0.0940** (0.0225) (0.0219) (0.0230) (0.0230) (0.0231) (0.0230) (0.0439) (0.0437) Day -0.0003 -0.0005 -0.0007* -0.0019 -0.0009* -0.0019 -0.0006 -0.0006 (0.0005) (0.0004) (0.0004) (0.0013) (0.0005) (0.0013) (0.0004) (0.0006) Labour PID 0.2102*** 0.1726*** 0.1726*** 0.1652*** 0.1703*** 0.2102*** 0.2089*** (0.0066) (0.0066) (0.0065) (0.0152) (0.0152) (0.0066) (0.0145) No Maj. Pty. PID 0.0095 0.0105 0.0094 0.0104 0.0094 0.0099 0.0099 (0.0212) (0.0219) (0.0220) (0.0219) (0.0220) (0.0213) (0.0212) PEP 0.2378*** (0.0177) 0.2041*** (0.0306) 0.2379*** (0.0176) 0.2054*** (0.0315) PEP*Day 0.0022 (0.0022) 0.0021 (0.0023) Lab. PID*Day 0.0005 (0.0008) 0.0001 ' (0.0009) 0.0001 (0.0008) Unemp.*Day 0.0020 (0.0026) 0.0020 (0.0026) Constant 0.5850*** 0.4754*** 0.3590*** 0.3768*** • 0.3621*** 0 3771*** 0.4764*** 0.4769*** (0.0167) (0.0148) (0.0169) (0.0240) (0.0179) (0.0240) (0.0150) (0.0163) Observations 4654 4602 4550 4550 4550 4550 4602 4602 R-squared 0.01 0.16 0.21 0.21 0.21 0.21 0.16 0.16 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.20. NEP Models, General Estimates, United States 2000 (1) (2) (3) (4) (5) (6) (7) (8) (9) Male 0.0532*** 0.0586*** 0.0528*** 0.0528*** 0.0528*** 0.0528*** 0.0585*** 0.0586*** 0.0585*** (0.0039) (0.0039) (0.0037) (0.0037) (0.0037) (0.0037) (0.0039) (0.0039) (0.0039) Black -0.0803*** -0.0946*** -0.0866*** -0.0866*** -0.0865*** -0.0865*** -0.0946*** -0.0947*** -0.0946*** (0.0073) (0.0072) (0.0066) (0.0066) (0.0066) (0.0066) (0.0073) (0.0072) (0.0072) Evangelical -0.0280*** -0.0271*** -0.0305*** -0.0304*** -0.0304*** -0.0304*** -0.0271*** -0.0271*** -0.0270*** (0.0041) (0.0040) (0.0037) (0.0037) (0.0037) (0.0037) (0.0040) (0.0040) (0.0040) Union -0.0143*** -0.0174*** -0.0136** -0.0136** -0.0136** -0.0136** -0.0174*** -0.0174*** -0.0174*** (0.0052) (0.0052) (0.0051) (0.0051) (0.0051) (0.0051) (0.0052) (0.0052) (0.0052) Unemployed -0.0450*** -0.0415** 0.0043 0.0043 0.0043 0.0043 -0.0362 -0.0416** -0.0341 (0.0169) (0.0167) (0.0160) (0.0160) (0.0161) (0.0161) (0.0344) (0.0166) (0.0349) Income 0.2641*** 0.2646*** 0.0965*** 0.0965*** 0.0964*** 0.0964*** 0.2646*** 0.2814*** 0.2794*** (0.0085) (0.0084) (0.0085) (0.0085) (0.0085) (0.0085) (0.0083) (0.0168) (0.0171) Day -0.0001 -0.0002* -0.0001 -0.0002 -0.0003** -0.0004 -0.0002* 0.0001 -0.0001 (0.0001) (0.0001) (0.0001) (0.0003) (0.0001) (0.0003) (0.0001) (0.0002) (0.0002) Democrat PID 0.0369*** 0.0303*** 0.0303*** 0.0157** 0.0157** 0.0369*** 0.0369*** 0.0214** (0.0052) (0.0048) (0.0048) (0.0077) (0.0077) (0.0052) • (0.0052) (0.0084) No PID -0.0267*** -0.0208*** -0.0208*** -0.0209*** -0.0209*** -0.0267*** -0.0268*** -0.0270*** (0.0042) (0.0040) (0.0040) (0.0040) (0.0040) (0.0042) (0.0042) (0.0042) PEP 0.3891*** (0.0082) 0.3838*** (0.0199) 0.3891*** (0.0082) 0.3838*** (0.0200) PEP*Day 0.0002 (0.0005) 0.0002 (0.0005) Dem. PID*Day 0.0004** (0.0002) 0.0004** (0.0002) 0.0005** (0.0002) Unemp.*Day -0.0002 (0.0009) -0.0002 (0.0009) Income*Day -0.0005 (0.0005) -0.0005 (0.0005) Constant 0.4628*** 0.4625*** 0.3312*** 0.3341*** 0.3358*** 0.3387*** 0.4624*** 0.4543*** 0.4600*** (0.0066) (0.0074) (0.0080) (0.0127) (0.0085) (0.0131) (0.0074) (0.0106) (0.0113) Observations 17382 17382 17382 17382 17382 17382 17382 17382 17382 R-squared 0.10 0.11 0.22 0.22 0.22 0.22 0.11 0.11 0.11 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 7o Table A2.21, NEP Models, High Sophistication Estimates, Canada 1988 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.0581*** -0.0540*** -0.0473*** -0.0472*** -0.0472*** -0.0472*** -0.0540*** -0.0540*** -0.0538*** (0.0123) (0.0121) (0.0122) (0.0122) (0.0122) (0.0122) (0.0121) (0.0121) (0.0121) > 55 yrs. 0.0034 0.0020 0.0178 0.0175 0.0177 0.0175 0.0021 0.0024 0.0024 (0.0128) (0.0129) (0.0133) (0.0133) (0.0133) (0.0133) (0.0129) (0.0129) (0.0130) Non-European 0.0181 0.0251 0.0236 0.0237 0.0236 0.0238 0.0254 0.0248 0.0254 (0.0244) (0.0240) (0.0229) (0.0230) (0.0229) (0.0230) (0.0242) (0.0239) (0.0240) French Speaker -0.0070 -0.0090 -0.0100 -0.0098 -0.0100 -0.0098 -0.0092 -0.0095 -0.0099 (0.0208) (0.0211) (0.0220) (0.0219) (0.0220) (0.0220) (0.0211) (0.0211) (0.0213) Catholic -0.0010 0.0092 0.0068 0.0064 0.0068 0.0065 0.0094 0.0094 0.0098 (0.0145) (0.0146) (0.0137) (0.0137) (0.0137) (0.0137) (0.0147) (0.0146) (0.0147) Non-religious -0.0094 -0.0023 -0.0109 -0.0109 -0.0108 -0.0108 -0.0022 -0.0023 -0.0018 (0.0218) (0.0205) (0.0190) (0.0190) (0.0190) (0.0190) (0.0205) (0.0204) (0.0205) West -0.0064 -0.0052 -0.0023 -0.0025 -0.0024 -0.0026 -0.0052 -0.0055 -0.0056 (0.0164) (0.0161) (0.0157) (0.0156) (0.0156) (0.0155) (0.0161) (0.0163) (0.0161) Quebec 0.0448* 0.0503** 0.0499** 0.0498** 0.0499** 0.0498** 0.0505** 0.0506** 0.0508** (0.0238) (0.0228) (0.0238) (0.0238) (0.0238) (0.0238) (0.0228) (0.0227) (0.0228) Atlantic 0.0243 0.0220 0.0201 0.0199 0.0201 0.0199 0.0219 0.0219 0.0216 (0.0203) (0.0196) (0.0187) (0.0187) (0.0187) (0.0187) (0.0197) (0.0196) (0.0197) Degree 0.0312** 0.0371*** 0.0349*** 0.0353*** 0.0350*** 0.0353*** 0.0371*** 0.0368*** 0.0369*** (0.0139) (0.0129) (0.0127) (0.0127) (0.0127) (0.0128) (0.0129) (0.0127) (0.0129) Unemployed -0.0259 -0.0296 -0.0105 -0.0108 -0.0102 -0.0106 -0.0430 -0.0297 -0.0475 (0.0192) (0.0182) (0.0192) (0.0191) (0.0196) (0.0194) (0.0447) (0.0182) (0.0438) Union -0.0258** -0.0190 -0.0141 -0.0141 -0.0141 -0.0141 -0.0190 -0.0195 -0.0193 (0.0125) (0.0129) (0.0119) (0.0119) (0.0119) (0.0119) (0.0129) (0.0130) (0.0129) Income 0.0561** 0.0432** 0.0260 0.0258 0.0262 0.0260 0.0432** 0.0143 0.0145 (0.0214) (0.0210) (0.0214) (0.0213) (0.0212) (0.0211) (0.0211) (0.0426) (0.0442) Day 0.0006 0.0006 0.0005 0.0001 0.0005 0.0001 0.0006 0.0000 -0.0002 (0.0004) (0.0004) (0.0004) (0.0010) (0.0006) (0.0010) (0.0005) (0.0009) (0.0009) PC PID 0.0963*** 0.0862*** 0.0859*** 0.0824*** 0.0832*** 0.0965*** 0.0966*** 0.0831*** (0.0154) (0.0141) (0.0140) (0.0268) (0.0269) . (0.0156) (0.0153) (0.0299) No PID 0.0108 0.0141 0.0140 0.0140 0.0139 0.0107 0.0104 0.0102 . (0.0148) (0.0147) . (0.0147) (0.0147) (0.0147) (0.0148) (0.0147) (0.0147) PEP 0.1565*** (0.0242) 0.1366*** (0.0489) 0.1562*** (0.0237) 0.1370*** (0.0493) PEP*Day 0.0007 (0.0018) 0.0007 (0.0018) PC PID*Day 0.0001 (0.0009) 0.0001 (0.0009) 0.0005 (0.0010) Unemp.*Day 0.0005 (0.0014) 0.0007 (0.0013) VO 4^ (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0011 0.0011 (0.0018) (0.0018) Constant 0.5585*** 0.5219*** 0.4396*** 0.4512*** 0.4408*** 0.4517*** 0.5222*** 0.5367*** 0.5410*** (0.0249) (0.0243) (0.0276) (0.0339) (0.0275) (0.0340) (0.0246) (0.0332) (0.0332) Observations 1524 1524 1524 1524 1524 1524 1524 1524 ' 1524 R-squared 0.06 0.10 0.14 0.14 0.14 0.14 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.22. NEP Models, High Sophistication Estimates, Canada 1993 (1) (2) "(3) (4) Woman -0.0610*** -0.0567*** -0.0530*** -0.0537*** (0.0169) (0.0166) (0.0172) (0.0173) > 55 yrs. -0.0041 -0.0010 0.0086 0.0090 (0.0183) (0.0184) (0.0178) (0.0178) Non-European 0.0288 0.0342 0.0367 0.0390 (0.0335) (0.0339) (0.0356) (0.0357) French Speaker -0.0218 -0.0207 -0.0297 -0.0294 (0.0288) (0.0282) (0.0288) (0.0287) Catholic -0.0196 -0.0142 -0.0110 -0.0108 (0.0207) (0.0215) (0.0217) (0.0216) Non-religious 0.0216 0.0282 0.0291 0.0291 (0.0241) (0.0243) (0.0251) (0.0251) West 0.0230 0.0215 0.0133 0.0137 (0.0176) (0.0169) (0.0176) (0.0178) Quebec -0.0069 -0.0057 -0.0028 -0.0029 (0.0340) (0.0331) (0.0341) (0.0340) Atlantic 0.0650* 0.0622* 0.0544 0.0561 (0.0350) (0.0350) (0.0345) (0.0349) Degree 0.0308 0.0290 0.0249 0.0258 (0.0197) (0.0192) (0.0193) (0.0192) Unemployed -0.0396 -0.0431 -0.0127 -0.0141 (0.0437) (0.0451) (0.0430) (0.0440) Union -0.0482*** -0.0439*** -0.0413** -0.0415** (0.0169) (0.0162) (0.0164) (0.0165) Income 0.0608* 0.0467 0.0417 0.0413 (0.0358) (0.0358) (0.0346) (0.0345) Day -0.0004 -0.0002 -0.0002 -0.0014 (0.0007) (0.0007) (0.0007) (0.0010) PC PID 0.0697*** 0.0602*** 0.0608*** (0.0197) (0.0208) (0.0206) No PID -0.0124 -0.0096 -0.0096. (0.0182) (0.0183) (0.0185) PEP 0.1390*** (0.0268) 0.0775* (0.0428) PEP*Day ' 0.0028 (0.0019) PC PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.0530*** -0.0537*** -0.0562*** -0.0561*** -0.0557*** (0.0174) (0.0175) (0.0167) (0.0168) (0.0170) 0.0078 0.0083 -0.0006 0.0003 -0.0000 (0.0180) (0.0179) (0.0185) (0.0184) (0.0186) 0.0373 0.0394 0.0338 0.0359 0.0358 (0.0354) (0.0356) (0.0335) (0.0342) (0.0336) -0.0303 -0.0300 -0.0201 -0.0223 -0.0220 (0.0287) (0.0285) (0.0284) (0.0283) (0.0284) -0.0096 -0.0095 -0.0143 -0.0136 -0.0128 (0.0212) (0.0211) (0.0215) (0.0216) (0.0212) 0.0304 0.0303 0.0286 0.0287 0.0299 (0.0249) (0.0249) (0.0241) (0.0245) (0.0241) 0.0134 0.0137 0.0217 0.0216 0.0219 (0.0177) (0.0178) (0.0169) (0.0171) (0.0171) -0.0026 -0.0028 -0.0047 -0.0047 -0.0039 (0.0342) (0.0340) (0.0332) (0.0328) (0.0330) 0.0548 0.0563 0.0634* 0.0614* 0.0628* (0.0347) (0.0351) (0.0352) (0.0346) (0.0350) 0.0245 0.0253 0.0288 0.0292 0.0287 (0.0193) (0.0193) (0.0192) (0.0192) (0.0192) -0.0131 -0.0143 -0.0016 -0.0426 -0.0065 (0.0425) (0.0434) (0.0924) (0.0460) (0.0967) -0.0414** -0.0416** -0.0432** -0.0431** -0.0426** (0.0164) (0.0164) (0.0162) (0.0162) (0.0160) 0.0402 0.0399 0.0467 -0.0254 -0.0199 (0.0338) (0.0337) (0.0358) (0.0646) (0.0672) -0.0006 -0.0016 -0.0001 -0.0019 -0.0019 (0.0009) (0.0011) (0.0007) (0.0013) (0.0015) 0.0280 0.0318 0.0700*** 0.0692*** 0.0477 (0.0406) (0.0402) (0.0194) (0.0194) (0.0394) -0.0103 -0.0102 -0.0122 -0.0104 -0.0109 (0.0183) (0.0186) (0.0182) (0.0182) (0.0183) 0.1396*** 0.0821* (0.0270) (0.0429) 0.0026 (0.0019) 0.0015 0.0014 0.0010 (0.0015) (0.0015) (0.0015) -0.0020 -0.0018 (0.0033) (0.0034) (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0033 0.0030 (0.0022) (0.0022) Constant 0.3110*** 0.2942*** 0.2401*** 0.2647*** 0.2485*** 0.2705*** 0.2906*** 0.3290*** 0.3285*** (0.0284) (0.0280) (0.0309) (0.0348) (0.0328) (0.0360) (0.0292) (0.0370) (0.0410) Observations 1088 1088 1088 1088 1088 1088 1088 1088 1088 R-squared 0.06 0.07 0.10 0.10 0.10 0.10 0.07 0.08 0.08 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.23. NEP Models, High Sophistication Estimates, Canada 1997 (1) (2) (3) (4) Woman -0.1073*** -0.1098*** -0.0975*** -0.0974*** (0.0206) (0.0212) (0.0212) (0.0212) > 55 yrs. 0.0088 0.0051 0.0150 0.0154 (0.0205) (0.0202) (0.0202) (0.0204) Non-European -0.0112 -0.0153 -0.0166 -0.0158 (0.0424) (0.0408) (0.0421) (0.0422) French Speaker -0.0691** -0.0548* -0.0525 -0.0524 (0.0313) (0.0319) (0.0316) (0.0317) Catholic -0.0175 -0.0282 -0.0263 -0.0261 (0.0264) (0.0261) (0.0257) (0.0256) Non-religious 0.0115 0.0054 0.0016 0.0018 (0.0249) (0.0248) (0.0247) (0.0244) West -0.0438* -0.0322 -0.0279 -0.0270 (0.0236) (0.0232) (0.0230) (0.0229) Quebec 0.0384 0.0398 0.0463 0.0471 (0.0368) (0.0367) (0.0370) (0.0371) Atlantic -0.0774** -0.0709* -0.0585 -0.0573 (0.0377) (0.0366) (0.0360) (0.0365) Degree 0.0462* 0.0458* 0.0452* . 0.0444* (0.0251) (0.0256) (0.0255) (0.0258) Unemployed -0.1313** -0.1281** -0.0816 -0.0786 (0.0570) (0.0563) (0.0521) (0.0521) Union -0.0682*** -0.0660*** -0.0518** -0.0516** (0.0189) (0.0187) (0.0192) (0.0191) Income 0.1683*** 0.1661*** 0.1367*** 0.1382*** (0.0379) (0.0376) (0.0389) (0.0387) Day 0.0006 0.0005 0.0006 -0.0012 (0.0012) (0.0012) (0.0012) (0.0018) Liberal PID 0.0688*** 0.0680*** 0.0686*** (0.0219) (0.0221) (0.0220) No PID 0.0027 0.0028 0.0034 (0.0260) (0.0262) (0.0261) PEP 0.2525*** (0.0450) 0.1767* (0.0936) PEP*Day 0.0038 (0.0038) Lib. PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.0978*** -0.0977*** -0.1098*** -0.1098*** -0.1101*** (0.0211) (0.0212) (0.0211) (0.0212) (0.0211) 0.0143 0.0147 0.0049 0.0051 0.0043 (0.0204) (0.0206) (0.0203) (0.0202) (0.0204) -0.0180 -0.0173 -0.0171 -0.0153 -0.0184 (0.0425) (0.0426) (0.0420) (0.0410) (0.0424) -0.0534* -0.0535* -0.0561* -0.0548* -0.0572* (0.0311) (0.0312) (0.0319) (0.0319) (0.0315) -0.0254 -0.0250 -0.0279 -0.0282 -0.0269 (0.0257) (0.0255) (0.0262) (0.0264) (0.0262) 0.0013 0.0015 0.0052 0.0054 0.0047 (0.0244) (0.0242) (0.0247) . (0.0248) (0.0244) -0.0277 -0.0267 -0.0321 -0.0322 -0.0319 (0.0232) (0.0232) (0.0231) (0.0232) (0.0233) 0.0464 0.0472 0.0403 0.0398 0.0404 (0.0370) (0.0372) (0.0367) (0.0366) (0.0367) -0.0575 -0.0561 -0.0712* -0.0709* -0.0701* (0.0364) (0.0369) (0.0364) (0.0362) (0.0366) 0.0455* 0.0447* 0.0457* 0.0458* 0.0460* (0.0256) (0.0258) (0.0256) (0.0258) (0.0259) -0.0821 -0.0791 -0.2495 -0.1281** -0.2491 (0.0522) (0.0521) (0.1767) (0.0562) (0.1769) -0.0514** -0.0512** -0.0655*** -0.0660*** -0.0650*** (0.0193) (0.0191) (0.0187) (0.0187) (0.0186) 0.1366*** 0.1381*** 0.1660*** 0.1660** 0.1589** (0.0389) (0.0387) (0.0378) (0.0671) (0.0680) 0.0010 -0.0009 0.0004 0.0005 0.0007 (0.0009) (0.0019) (0.0012) (0.0019) (0.0018) 0.0916 0.0952* 0.0691*** 0.0688*** 0.0956* (0.0571). (0.0551) (0.0220) (0.0219) (0.0541) 0.0033 0.0040 0.0032 0.0027 0.0040 (0.0263) (0.0261) (0.0257) (0.0262) (0.0259) 0.2521*** 0.1724* (0.0451) (0.0918) 0.0040 (0.0037) -0.0012 -0.0013 -0.0013 (0.0024) (0.0024) (0.0023) 0.0057 0.0056 (0.0072) (0.0073) OO (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0000 0.0003 (0.0036) (0.0036) Constant 0.6380*** 0.6162*** . 0.4891*** 0.5236*** 0.4814*** 0.5166*** 0.6188*** 0.6163*** 0.6133*** (0.0375) (0.0355) (0.0430) (0.0543) (0.0443) (0.0577) (0.0370) (0.0376) (0.0412) Observations 1577 1577 1577 1577 1577 1577 1577 1577 1577 R-squared 0.09 0.10 0.12 0.13 0.12 0.13 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.24. NEP Models, High Sophistication Estimates, Canada 2000 (1) (2) (3) (4) Woman -0.0673*** -0.0715*** -0.0684*** -0.0684*** (0.0138) (0.0139) (0.0141) (0.0141) > 55 yrs. 0.0213 0.0194 0.0390* 0.0390* (0.0199) (0.0199) - (0.0194) (0.0195) Non-European 0.0361* 0.0318 0.0242 0.0242 (0.0208) (0.0203) (0.0198) (0.0199) French Speaker -0.0181 -0.0092 -0.0118 -0.0118 (0.0271) (0.0264) (0.0273) (0.0273) Catholic 0.0044 -0.0049 0.0010 0.0010 (0.0247) (0.0246) (0.0247) (0.0247) Non-religious -0.0072 -0.0040 -0.0032 -0.0032 (0.0275) (0.0278) (0.0266) (0.0271) West -0.1128*** -0.1014*** -0.0884*** -0.0884*** (0.0226) (0.0227) (0.0217) (0.0213) Quebec -0.0004 0.0051 0.0108 0.0108 (0.0219) (0.0229) (0.0229) (0.0228) Atlantic -0.0750*** -0.0684** -0.0668*** -0.0668*** (0.0263) (0.0253) (0.0228) (0.0227) Degree 0.0471* 0.0464* 0.0337 0.0337 (0.0243) (0.0239) (0.0243) (0.0244) Unemployed -0.1092** -0.0995** -0.0609 -0.0608 (0.0432) (0.0430) (0.0449) (0.0451) Union -0.0002 0.0018 0.0104 0.0104 (0.0148) (0.0150) (0.0143) (0.0143) Income 0.1023*** 0.0961*** 0.0749*** 0.0749*** (0.0224) (0.0214) (0.0193) (0.0193) Day -0.0006 -0.0006 -0.0004 -0.0005 (0.0008) (0.0008) (0.0008) (0.0020) Liberal PID 0.0756*** 0.0538** 0.0538** (0.0232) (0.0226) (0.0226) No PID -0.0053 -0.0059 -0.0058 (0.0231) (0.0229) (0.0228) PEP 0.2071*** (0.0298) 0.2052*** (0.0545) PEP*Day 0.0001 (0.0029) Lib. PID*Day Unemp.*Day (5) (6) (7) (8) (9) -0.0685*** -0.0685*** -0.0714*** -0.0715*** -0.0715*** (0.0140) (0.0140) (0.0139) (0.0139) (0.0138) 0.0387* 0.0388* 0.0196 0.0194 0.0193 (0.0193) (0.0193) (0.0198) (0.0200) (0.0198) 0.0246 0.0245 0.0318 0.0318 0.0322 (0.0197) (0.0198) (0.0203) (0.0203) (0.0202) -0.0134 -0.0136 -0.0091 -0.0092 -0.0108 (0.0271) (0.0271) (0.0267) (0.0264) (0.0266) 0.0010 0.0011 -0.0051 -0.0049 -0.0051 (0.0246) (0.0246) (0.0246) (0.0245) (0.0245) -0.0030 -0.0027 -0.0041 • -0.0040 -0.0039 (0.0267) (0.0272) (0.0278) (0.0278) (0.0279) -0.0879*** -0.0881*** -0.1014*** -0.1014*** -0.1008*** (0.0216) (0.0213) (0.0227) (0.0227) (0.0226) 0.0116 0.0115 0.0050 0.0050 0.0058 (0.0225) (0.0225) (0.0230) (0.0231) (0.0229) -0.0664*** -0.0666*** -0.0685**. -0.0684** -0.0681** (0.0228) (0.0227) (0.0252) (0.0253) (0.0253) 0.0340 0.0340 0.0464* 0.0464* 0.0467* (0.0243) (0.0245) (0.0240) (0.0240) (0.0241) -0.0617 -0.0613 -0.0806 -0.0995** -0.0764 (0.0450) (0.0452) (0.0874) (0.0430) (0.0870) 0.0102 0.0102 0.0020 0.0018 0.0018 (0.0142) (0.0142) (0.0149) (0.0150) (0.0148) 0.0739*** 0.0738*** 0.0961*** 0.0965** 0.0926** (0.0196) (0.0195) (0.0214) (0.0372) (0.0369) 0.0002 -0.0001 -0.0006 -0.0006 0.0001 (0.0008) (0.0019) (0.0008) (0.0012) (0.0011) 0.0932*** 0.0944*** 0.0756*** 0.0756*** 0.1189*** (0.0291) (0.0295) (0.0233) (0.0233) (0.0302) -0.0058 -0.0057 -0.0051 -0.0053 -0.0050 (0.0229) (0.0228) (0.0232) (0.0231) (0.0232) 0.2068*** 0.1963*** (0.0295) (0.0544) 0.0005 (0.0029) -0.0020 -0.0021 -0.0022 (0.0013) (0.0014) (0.0015) -0.0010 -0.0013 (0.0043) (0.0043) O O (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day -0.0000 0.0001 (0.0017) (0.0017) Constant 0.6979*** 0.6768*** 0.5648*** 0.5659*** 0.5532*** 0.5586*** 0.6760*** 0.6766*** 0.6641*** (0.0273) (0.0316) (0.0342) (0.0442) (0.0330) (0.0425) (0.0316) (0.0339) (0.0317) Observations 2069 2069 2069 2069 2069 2069 2069 2069 2069 R-squared 0.06 0.07 0.11 0.11 0.11 0.11 0.07 0.07 0.07 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.25. NEP Models, High Sophistication Estimates, Canada 2004 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.0472* -0.0523** -0.0469** -0.0470** -0.0485** -0.0485** -0.0528** -0.0514** -0.0534** (0.0233) (0.0224) (0.0209) (0.0210) (0.0206) (0.0206) (0.0226) (0.0216) (0.0215) > 55 yrs. 0.0348 0.0320 0.0427* 0.0427* 0.0396 0.0396 0.0318 0.0300 0.0266 (0.0267) (0.0253) (0.0246) (0.0247) (0.0242) (0.0242) (0.0253) (0.0250) (0.0245) Non-European 0.1069** 0.0738 0.0436 0.0437 0.0468 0.0468 0.0738 0.0748 0.0780 (0.0493) (0.0487) (0.0444) (0.0444) (0.0441) (0.0441) (0.0487) (0.0484) (0.0482) French Speaker 0.0289 0.0547 0.0504 0.0502 0.0515 0.0515 0.0553 0.0570 . 0.0587 (0.0437) (0.0415) (0.0421) (0.0421) (0.0423) (0.0423) (0.0409) (0.0414) (0.0412) Catholic 0.0190 0.0075 0.0101 0.0103 0.0119 0.0119 0.0084 0.0080 0.0106 (0.0264) (0.0261) (0.0260) (0.0260) (0.0262) (0.0262) (0.0272) (0.0259) (0.0273) Non-religious 0.0210 0.0269 0.0210 0.0207 0.0181 0.0181 0.0272 0.0265 0.0236 (0.0271) (0.0277) (0.0278) (0.0276) (0.0273) (0.0271) (0.0276) (0.0274) (0.0270) West 0.0018 0.0178 0.0096 0.0097 0.0117 0.0117 0.0185 0.0162 0.0189 (0.0272) (0.0287) (0.0283) (0.0282) (0.0277) (0.0277) (0.0290) (0.0284) (0.0283) Quebec 0.0001 -0.0026 -0.0121 -0.0122 -0.0124 -0.0124 -0.0029 -0.0085 -0.0090 (0.0452) (0.0431) (0.0420) (0.0420) (0.0417) (0.0417) (0.0428) (0.0444) (0.0442) Atlantic 0.0187 0.0295 0.0118 0.0116 0.0117 0.0117 0.0300 0.0269 0.0272 (0.0458) (0.0425) (0.0423) (0.0422) (0.0412) (0.0412) (0.0425) (0.0426) (0.0415) Degree 0.0769*** 0.0780*** 0.0581** 0.0582** 0.0577** 0.0577** 0.0781*** 0.0796*** 0.0792*** (0.0223) (0.0223) (0.0232) (0.0231) (0.0231) (0.0230) (0.0222) (0.0224) (0.0222) Unemployed 0.0024 0.0215 0.0359 0.0372 0.0372 0.0374 0.0847 0.0241 0.0744 (0.0763) (0.0781) (0.0803) (0.0807) (0.0821) (0.0820) (0.1337) (0.0787) (0.1442) Union 0.0025 -0.0024 0.0015 0.0015 0.0010 0.0010 -0.0026 -0.0027 -0.0033 (0.0280) (0.0286) (0.0282) (0.0282) (0.0284) (0.0284) (0.0286) (0.0290) (0.0292) Income 0.0859** 0.0884** 0.0684 0.0685 0.0687 0.0687 0.0879** -0.0640 -0.0639 (0.0416) (0.0406) (0.0420) (0.0421) (0.0421) (0.0422) (0.0410) (0.0654) (0.0670) Day 0.0048*** 0.0050*** 0.0047*** 0.0051** 0.0060*** 0.0060*** 0.0050*** 0.0004 0.0019 (0.0010) (0.0010) (0.0009) (0.0020) (0.0012) (0.0019) (0.0010) (0.0019) (0.0022) Liberal PID 0.1297*** 0.1025*** 0.1023*** 0.1747*** 0.1744*** 0.1300*** 0.1287*** 0.2060*** (0.0285) (0.0286) (0.0288) (0.0553) ' (0.0584) (0.0288) (0.0281) (0.0537) No PID 0.0380 0.0395 0.0393 0.0404 0.0404 0.0384 0.0367 0.0379 (0.0272) (0.0273) (0.0271) (0.0271) (0.0269) (0.0272) (0.0277) (0.0275) PEP 0.1988*** (0.0285) 0.2172*** (0.0764) 0.1984*** (0.0291) 0.2017** (0.0838) PEP*Day -0.0009 (0.0029) -0.0002 (0.0032) Lib. PID*Day -0.0037* (0.0021) -0.0037 (0.0023) -0.0040* (0.0022) Unemp.*Day -0.0037 -0.0028 (0.0092) (0.0095) to O to (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0079** 0.0078** (0.0030) (0.0031) Constant 0.3904*** 0.3312*** 0.2725*** 0.2638*** 0.2480*** 0.2466*** 0.3296*** 0.4212*** 0.3936*** (0.0507) (0.0544) (0.0575) (0.0711) (0.0610) (0.0718) (0.0545) (0.0672) (0.0721) Observations 1132 1132 1132 1132 1132 1132 1132 1132 1132 R-squared 0.06 0.08 0.12 0.12 0.12 0.12 0.08 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O Table A2.26. NEP Models, High Sophistication Estimates, New Zealand 1996 (1) (2) (3) (4) (5) (6) Woman -0.0738** -0.0576** -0.0574** -0.0543* -0.0570** -0.0530* (0.0290) (0.0280) ' (0.0279) (0.0279) (0.0278) (0.0277) Age -0.0028** -0.0029** -0.0029** -0.0030** -0.0029** -0.0030** (0.0013) (0.0011) (0.0011) (0.0011) (0.0011) (0.0011) Homeowner 0.0880* 0.0797 0.0800 0.0760 0.0799 0.0766 (0.0519) (0.0492) (0.0496) (0.0495) (0.0495) (0.0502) Working Class 0.0066 0.0383 0.0386 0.0378 0.0382 0.0379 (0.0540) (0.0471) (0.0475) (0.0476) (0.0470) (0.0479) Degree 0.0468 0.0466 0.0469 0.0465 0.0464 0.0463 (0.0457) (0.0430) (0.0431) (0.0429) (0.0430) (0.0431) Union -0.0500 -0.0268 -0.0276 -0.0315 -0.0254 -0.0300 (0.0370) (0.0369) (0.0379) (0.0366) (0.0378) (0.0383) Public Sector Employee 0.0194 0.0291 0.0293 0.0300 0.0289 0.0299 (0.0273) (0.0253) (0.0255) (0.0255) (0.0253) (0.0257) Unemployed , 0.1295 0.1891* 0.1880* -0.4915 0.1912* -0.5106 (0.0924) (0.0937) (0.0931) (0.3681) (0.0952) (0.3668) Income 0.1588** 0.1591*** 0.1595*** 0.1574*** 0.1292 0.1084 (0.0620) (0.0564) (0.0565) (0.0566) (0.0874) (0.0889) Day 0.0044*** 0.0039*** 0.0042*** 0.0038*** 0.0027 0.0020 (0.0012) (0.0012) (0.0013) (0.0012) (0.0031) (0.0032) National PID 0.1922*** 0.2053*** 0.1937*** 0.1922*** 0.2049*** (0.0393) (0.0651) (0.0400) (0.0392) (0.0647) No PID 0.0422 0.0413 0.0442 0.0417 0.0426 (0.0350) (0.0352) (0.0345) (0.0350) (0.0349) National PID*Day . -0.0007 (0.0026) -0.0006 (0.0026) Unemployed*Day 0.0297** (0.0144) 0.0306** (0.0143) Income*Day 0.0016 (0.0043) 0.0027 (0.0045) Constant 0.3696*** 0.2969*** 0.2930*** 0.3065*** 0.3194*** 0.3404*** (0.0856) (0.0766) (0.0783) (0.0787) (0.0732) (0.0784) Observations 334 333 333 333 333 333 R-squared 0.14 0.21 0.21 0.22 0.21 0.22 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% t-O o Table A2.27. NEP Models, High Sophistication Estimates, New Zealand 1999 (1) (2) (3) (4) (5) (6) Woman -0.0388 -0.0407 -0.0402 -0.0415 -0.0381 -0.0382 (0.0396) (0.0351) (0.0354) (0.0350) (0.0345) (0.0346) Age -0.0005 -0.0007 -0.0008 -0.0007 -0.0007 -0.0007 (0.0016) (0.0015) (0.0015) (0.0015) (0.0015) (0.0015) Maori -0.0152 0.0106 0.0088 0.0084 0.0113 0.0063 (0.0856) (0.0877) (0.0879) (0.0864) (0.0871) (0.0864) Degree -0.0416 -0.0241 -0.0238 -0.0276 -0.0259 -0.0285 (0.0396) (0.0379) (0.0385) (0.0384) (0.0374) (0.0387) Union -0.0150 0.0010 -0.0006 0.0014 -0.0013 -0.0033 (0.0534) (0.0495) (0.0498) (0.0493) (0.0504) (0.0513) Public Sector Employee -0.0208 -0.0145 -0.0141 -0.0114 -0.0165 -0.0129 (0.0415) (0.0445). (0.0445) (0.0445) (0.0437) (0.0442) Manual Worker -0.0793 -0.0518 -0.0524 -0.0528 -0.0491 -0.0512 (0.0596) (0.0611) (0.0609) (0.0609) (0.0616) (0.0611) Farmer 0.0355 -0.0103 -0.0099 -0.0111 -0.0112 -0.0113 (0.0810) (0.0601) (0.0577) (0.0608) (0.0598) (0.0566) Unemployed -0.0929 -0.1267 -0.1268 -0.3439** -0.1281 -0.3193* (0.1169) (0.1220) (0.1235) (0.1387) (0.1210) (0.1728) Income 0.2197** 0.1545* 0.1528* 0.1574* 0.2403* 0.2360 (0.0886) (0.0811) (0.0804) (0.0830) (0.1327) (0.1559) Day 0.0022 0.0030 0.0026 0.0027 0.0058 0.0046 (0.0028) . (0.0026) (0.0030) (0.0027) (0.0047) (0.0057) National PID 0.1530*** 0.1259 0.1541*** 0.1519*** 0.1088 (0.0448) (0.0895) (0.0450) (0.0443) (0.0926) No PID 0.0164 0.0162 0.0175 0.0146 0.0153 (0.0412) (0.0414) (0.0415) (0.0412) (0.0417) National PID*Day 0.0017 (0.0043) 0.0027 (0.0046) Unemployed*Day 0.0116 (0.0080) 0.0102 (0.0102) Income*Day -0.0048 (0.0064) -0.0046 (0.0081) Constant 0.3808*** 0.3590*** 0.3716*** 0.3598*** 0.3085*** 0.3322*** (0.1159) (0.1083) (0.1050) (0.1094) (0.1104) (0.1118) Observations 219 219 219 219 219 219 R-squared 0.09 0.15 0.15 0.15 0.15 0.15 Robust standard errors in parenth :ses * significant at 10%; ** significant at 5%; *** significant at 1% o LA Table A2.28. NEP Models, High Sophistication Estimates, New Zealand 2002 (1) (2) (3) (4) (5) (6) Age -0.0003 -0.0003 -0.0003 -0.0003 -0.0003 -0.0002 (0.0008) (0.0008) (0.0008) (0.0008) (0.0008) (0.0008) Woman -0.0448* -0.0480** -0.0473* -0.0477** -0.0474** -0.0464* (0.0238) (0.0228) (0.0236) (0.0230) (0.0224) (0.0235) Manual Worker -0.0264 -0.0239 -0.0239 -0.0239 -0.0249 -0.0251 (0.0296) (0.0293) (0.0294) (0.0293) (0.0293) (0.0293) Union 0.0234 0.0030 0.0038 0.0028 0.0036 0.0039 (0.0277) (0.0278) (0.0287) (0.0278) (0.0281) (0.0291) Unemployed 0.0871 0.0761 0.0755 -0.0733 0.0706 -0.1049* (0.0772) (0.0908) (0.0914) (0.0575) (0.0970) (0.0617) Income -0.0490 -0.0357 -0.0345 -0.0353 -0.1060 -0.1151 (0.0639) (0.0607) (0.0604) (0.0606) (0.1124) (0.1179) Day -0.0017 -0.0017 -0.0016 -0.0018 -0.0035 -0.0038 (0.0016) (0.0016) (0.0019) (0.0016) (0.0031) (0.0036) Labour PID 0.0833*** 0.0929** 0.0851*** 0.0802*** 0.0882** (0.0256) (0.0344) (0.0257) (0.0248) (0.0368) No PID 0.0166 0.0164 0.0185 0.0157 0.0177 (0.0364) (0.0367) (0.0368) (0.0361) (0.0367) Labour PID*Day -0.0005 (0.0019) -0.0003 (0.0020) Unemployed*Day 0.0100 (0.0067) 0.0117* (0.0068) Income*Day 0.0036 (0.0055) 0.0042 (0.0058) Constant 0.7744*** 0.7435*** 0.7387*** 0.7425*** 0.7775*** 0.7782*** (0.0731) (0.0685) (0.0719) (0.0684) (0.0805) (0.0887) Observations 366 366 366 366 366 366 R-squared 0.03 0.06 0.06 0.06 0.06 0.06 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O OS Table A2.29. NEP Models, High Sophistication Estimates, Unitec Kingdom 2001 (1) (2) (3) (4) (5) (6) (7) • (8) Age 0.0006 0.0008** 0.0009** 0.0009** 0.0009** 0.0009** 0.0008** 0.0008** (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) Woman -0.0258** -0.0244** -0.0225** -0.0224** -0.0224** -0.0225** -0.0243** -0.0244** (0.0111) (0.0117) (0.0105) (0.0105) (0.0104) (0.0105) (0.0117) (0.0117) Homeowner -0.0574*** -0.0292** -0.0152 -0.0153 -0.0152 -0.0152 -0.0290** -0.0290** (0.0148) (0.0134) (0.0129) (0.0129) (0.0129) (0.0130) (0.0134) (0.0134) Southeast 0.0059 0.0286* 0.0259 0.0268 0.0260N\ 0.0267 0.0289* 0.0287* (0.0192) (0.0164) (0.0161) (0.0161) (0.0160) (0.0161) (0.0164) (0.0163) Southwest -0.0205 -0.0068 -0.0018 -0.0008 -0.0015 -0.0009 -0.0063 -0.0067 (0.0252) (0.0237) (0.0241) (0.0241) (0.0240) (0.0240) (0.0237) (0.0237) Midlands -0.0032 -0.0061 -0.0069 -0.0058 -0.0065 -0.0060 -0.0066 -0.0070 (0.0182) (0.0142) (0.0139) (0.0139) (0.0136) (0.0137) (0.0142) (0.0139) North 0.0105 -0.0075 -0.0086 -0.0078 -0.0085 -0.0079 -0.0063 -0.0065 (0.0172) (0.0144) (0.0143) (0.0143) (0.0143) (0.0143) (0.0145) (0.0145) Wales -0.0217 -0.0135 -0.0086 -0.0074 -0.0085 -0.0073 -0.0140 -0.0140 (0.0353) (0.0295) (0.0300) (0.0300) (0.0300) (0.0299) (0.0295) (0.0294) Scotland 0.0238 0.0178 0.0147 0.0160 0.0150 0.0159 0.0175 0.0172 (0.0202) (0.0185) (0.0174) (0.0175) (0.0173) (0.0174) (0.0186) (0.0184) Working Class 0.0220** 0.0023 0.0103 0.0102 0.0103 0.0103 0.0023 0.0023 (0.0098) (0.0097) (0.0091) (0.0091) (0.0091) (0.0091) (0.0097) (0.0097) Unemployed -0.0211 -0.0157 -0.0008 -0.0005 -0.0006 -0.0006 -0.0961 -0.0966* (0.0385) (0.0322) (0.0311) (0.0312) (0.0311) (0.0313) (0.0566) (0.0568) Day 0.0000 -0.0001 -0.0003 -0.0021 -0.0005 -0.0021 -0.0002 0.0000 (0.0007) (0.0006) (0.0006) (0.0020) (0.0010) (0.0020) (0.0006) (0.0010) Labour PID 0.2367*** 0.1905*** 0.1908*** 0.1850*** 0.1955*** 0.2370*** 0.2437*** (0.0089) (0.0083) (0.0083) (0.0195) (0.0184) (0.0089) (0.0194) No Maj. Pty. PID 0.0130 0.0129 0.0093 0.0129 0.0092 0.0157 0.0158 (0.0364) (0.0393) (0.0389) (0.0392) (0.0390) (0.0365) (0.0364) PEP 0.2578*** (0.0238) 0.2067*** (0.0480) 0.2580*** (0.0238) 0.2035*** (0.0486) PEP*Day 0.0033 (0.0030) 0.0035 (0.0030) Lab. PID*Day 0.0004 (0.0011) -0.0003 (0.0009) -0.0004 (0.0011) Unemp.*Day 0.0052 (0.0031) 0.0052 (0.0031) Constant 0.6027*** 0.4691*** 0.3312*** 0.3589*** 0.3335*** 0.3586*** 0.4700*** 0.4671*** (0.0267) (0.0260) (0.0274) (0.0401) (0.0290) (0.0402) (0.0261) (0.0289) Observations 2707 2679 2660 2660 2660 2660 2679 2679 R-squared 0.02 0.19 0.25 0.25 0.25 0.25 0.19 0.19 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O Table A2.30. NEP Models, High Sophistication Estimates, United States 2000 (1) (2) (3) (4) (5) (6) (7) (8) (9) Male 0.0419*** 0.0496*** 0.0479*** 0.0479*** 0.0479*** 0.0480*** 0.0501*** 0.0496*** 0.0501*** (0.0086) (0.0088) (0.0079) (0.0079) (0.0079) (0.0079) (0.0087) (0.0088) (0.0086) Black -0.1032*** -0.1261*** -0.1128*** -0.1128*** -0.1129*** -0.1128*** -0.1259*** -0.1262*** -0.1261*** (0.0192) (0.0191) (0.0169) (0.0169) (0.0168) (0.0169) (0.0191) (0.0191) (0.0191) Evangelical -0.0310*** -0.0225** -0.0223** -0.0223** -0.0222** -0.0223** -0.0227** -0.0225** -0.0226** (0.0102) (0.0101) (0.0101) (0.0101) (0.0101) (0.0101) (0.0101) (0.0101) (0.0101) Union -0.0258** -0.0337*** -0.0281** -0.0280** -0.0281** -0.0280** -0.0335*** -0.0336*** -0.0335*** (0.0121) (0.0121) (0.0112) (0.0112) (0.0112) (0.0112) (0.0122) (0.0121) (0.0122) Unemployed -0.0644 -0.0628 -0.0312 -0.0309 -0.0311 -0.0308 -0.2345** -0.0630 -0.2411*** (0.0414) (0.0411) (0.0353) (0.0352) (0.0354) (0.0353) (0.0899) (0.0411) (0.0891) Income 0.2324*** 0.2409*** 0.0755*** 0.0756*** 0.0757*** 0.0758*** 0.2405*** 0 2227*** 0.2127*** (0.0224) (0.0222) (0.0199) (0.0199) (0.0199) (0.0200) (0.0220) (0.0641) (0.0638) Day 0.0001 0.0001 -0.0001 0.0003 -0.0001 0.0002 0.0000 -0.0001 -0.0006 (0.0002) (0.0002) (0.0002) (0.0010) (0.0003) (0.0011) (0.0002) (0.0009) (0.0009) Democrat PID 0.0661*** 0.0524*** 0.0524*** 0.0408 0.0409 0.0662*** 0.0662*** 0.0414 (0.0102) (0.0090) (0.0090) (0.0267) (0.0266) (0.0103) (0.0102) (0.0333) No PID 0.0044 0.0022 0.0022 0.0020 0.0020 0.0043 0.0043 0.0038 (0.0092) (0.0081) (0.0081) (0.0081) (0.0081) (0.0093) (0.0092) (0.0093) PEP 0.3687*** (0.0206) 0.3912*** (0.0681) 0.3685*** (0.0208) 0.3910*** (0.0684) PEP*Day -0.0006 (0.0017) -0.0006 (0.0017) Dem. PID*Day 0.0003 (0.0006) 0.0003 (0.0006) 0.0006 (0.0007) Unemp.*Day 0.0045** (0.0021) 0.0047** (0.0021) Income*Day 0.0005 (0.0015) 0.0007 (0.0015) Constant 0.5128*** 0.4823*** 0.3651*** 0.3517*** 0.3689*** 0.3554*** 0.4854*** 0.4924*** 0.5091*** (0.0169) (0.0185) (0.0208) (0.0467) (0.0241) (0.0495) (0.0183) (0.0401) (0.0423) Observations 3112 3112 3112 3112 3112 3112 3112 3112 3112 R-squared 0.09 0.10 0.21 0.21 0.21 0.21 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O Table A2.31. NEP Models, Low Sophistication Estimates, Canada 1988 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.0508*** -0.0488*** -0.0498*** -0.0498*** -0.0497*** -0.0498*** -0.0484*** -0.0479*** -0.0477*** (0.0107) (0.0110) (0.0112) (0.0111) (0.0112) (0.0111) (0.0109) (0.0111) (0.0111) > 55 yrs. 0.0124 0.0081 0.0195 0.0193 0.0194 0.0193 0.0078 0.0059 0.0060 (0.0151) (0.0160) (0.0168) (0.0167) (0.0168) (0.0167) (0.0160) (0.0165) (0.0165) Non-European -0.0011 0.0010 0.0060 0.0061 0.0059 0.0061 0.0021 0.0007 0.0017 (0.0260) (0.0255) (0.0242) (0.0243) (0.0243) (0.0244) (0.0254) (0.0255) (0.0256) French Speaker 0.0106 0.0112 0.0110 0.0113 0.0110 0.0113 0.0121 0.0111 0.0118 (0.0192) (0.0181) (0.0167) (0.0166) (0.0167) (0.0167) (0.0182) (0.0180) (0.0181) Catholic -0.0109 -0.0091 -0.0070 -0.0062 -0.0072 -0.0063 -0.0107 -0.0094 -0.0107 (0.0137) (0.0135) (0.0130) (0.0131) (0.0130) (0.0131) (0.0134) (0.0131) (0.0130) Non-religious 0.0120 0.0173 0.0143 0.0141 0.0141 0.0141 0.0154 0.0161 0.0147 (0.0209) (0.0203) (0.0204) (0.0206) (0.0204) (0.0206) (0.0204) (0.0202) (0.0203) West -0.0256 -0.0314* -0.0256 -0.0245 -0.0255 -0.0245 -0.0304* -0.0310* -0.0301* (0.0158) (0.0162) (0.0158) (0.0157) (0.0159) (0.0158) (0.0162) (0.0161) (0.0162) Quebec 0.0244 0.0240 0.0260 0.0261 0.0260 0.0261 0.0250 0.0249 0.0257 (0.0239) (0.0232) (0.0224) (0.0223) (0.0225) (0.0223) (0.0231) (0.0229) (0.0228) Atlantic -0.0152 -0.0203 -0.0184 -0.0173 -0.0182 -0.0173 -0.0199 -0.0179 -0.0180 (0.0167) (0.0171) (0.0165) (0.0163) (0.0164) (0.0163) (0.0170) (0.0171) (0.0170) Degree 0.0138 0.0127 0.0055 0.0042 0.0054 0.0042 0.0124 0.0117 0.0116 (0.0219) (0.0217) (0.0219) (0.0221) (0.0219) (0.0221) (0.0215) (0.0216) (0.0215) Unemployed -0.0227 -0.0202 -0.0083 -0.0084 -0.0082 -0.0083 0.0607 -0.0207 0.0514 (0.0225) (0.0233) (0.0220) (0.0219) (0.0221) (0.0220) (0.0410) (0.0235) (0.0420) Union -0.0370** -0.0316** -0.0296* -0.0292* -0.0296* -0.0292* -0.0315** -0.0332** -0.0329** (0.0148) (0.0147) (0.0151) (0.0151) (0.0152) (0.0152) (0.0147) (0.0145) (0.0146) Income 0.0663*** 0.0556** 0.0457* 0.0467* 0.0455* 0.0467* 0.0551** -0.0087 -0.0014 (0.0203) (0.0212) (0.0230) (0.0233) (0.0230) (0.0233) (0.0210) (0.0347) (0.0345) Day 0.0005 0.0005 0.0003 -0.0009 0.0003 -0.0009 0.0007 -0.0006 -0.0003 (0.0005) (0.0005) (0.0005) (0.0012) (0.0005) (0.0012) (0.0005) (0.0007) (0.0007) PC PID ' 0.0428** 0.0331** 0.0330** 0.0285 0.0318 0.0418** 0.0416** 0.0433 (0.0163) (0.0162) (0.0164) (0.0250) (0.0253) (0.0163) (0.0165) (0.0267) No PID -0.0231 -0.0287 -0.0288 -0.0287 -0.0288 -0.0235 -0.0236 -0.0240 (0.0182) (0.0183) (0.0183) (0.0183) (0.0184) (0.0181) (0.0180) (0.0179) PEP 0.1183*** (0.0262) 0.0683 (0.0509) 0.1184*** (0.0263) 0.0685 (0.0508) PEP*Day 0.0022 (0.0017) 0.0022 (0.0017) PC PID*Day 0.0002 (0.0007) 0.0000 (0.0007) -0.0001 (0.0008) Unemp.*Day -0.0036** -0.0032** (0.0014) (0.0015) O V O (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0027** 0.0024* (0.0013) (0.0014) Constant 0.5486*** 0.5488*** 0.4898*** 0.5158*** 0.4911*** 0.5161*** 0.5448*** 0.5755*** 0.5681*** (0.0226) (0.0242) (0.0270) (0.0367) (0.0271) (0.0369) (0.0238) (0.0282) (0.0280) Observations 1273 1273 1273 1273 1273 1273 1273 1273 1273 R-squared 0.05 0.06 0.09 0.09 0.09 0.09 0.07 0.07 0.07 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.32. NEP Models, Low Sophistication Estimates, Canada 1993 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.0458*** • -0.0465*** -0.0448*** -0.0451*** -0.0450*** -0.0454*** -0.0465*** -0.0464*** -0.0466*** (0.0119) (0.0120) (0.0116) (0.0116) (0.0116) (0.0117) (0.0120) (0.0119) (0.0119) > 55 yrs. -0.0563*** -0.0584*** -0.0517*** -0.0518*** -0.0509*** -0.0509*** -0.0579*** -0.0586*** -0.0575*** (0.0137) (0.0137) (0.0139) (0.0139) (0.0139) (0.0140) (0.0137) (0.0137) (0.0139) Non-European -0.0204 -0.0183 -0.0185 -0.0197 -0.0179 -0.0192 -0.0183 -0.0187 -0.0181 (0.0190) (0.0193) (0.0191) (0.0188) (0.0190) (0.0188) (0.0194) (0.0192) (0.0194) French Speaker -0.0363 -0.0352 -0.0239 -0.0245 -0.0232 -0.0237 -0.0346 -0.0365 -0.0352 (0.0223) (0.0219) (0.0206) (0.0207) (0.0204) (0.0205) (0.0217) (0.0218) (0.0215) Catholic -0.0358** -0.0330** -0.0332** -0.0330** -0.0324** -0.0320** -0.0331** -0.0326** -0.0319** (0.0156) (0.0160) (0.0155) (0.0156) (0.0156) (0.0157) (0.0159) (0.0158) (0.0158) Non-religious 0.0455** 0.0504** 0.0435** 0.0432** 0.0442** 0.0438** 0.0516** 0.0502** 0.0517** (0.0207) (0.0208) (0.0208) (0.0209) (0.0207) (0.0208) (0.0208) (0.0206) (0.0205) West -0.0013 -0.0031 -0.0165 -0.0169 -0.0168 -0.0173 -0.0031 -0.0021 -0.0026 (0.0128) (0.0126) (0.0117) (0.0119) (0.0117) (0.0119) (0.0125) (0.0127) (0.0126) Quebec -0.0136 -0.0148 -0.0280 -0.0284 -0.0293 -0.0299 -0.0153 -0.0128 -0.0147 (0.0223) (0.0224) (0.0229) (0.0230) (0.0227) (0.0229) (0.0222) (0.0222) (0.0220) Atlantic 0.0099 0.0067 -0.0069 -0.0083 -0.0079 -0.0096 0.0064 0.0077 0.0064 (0.0209) (0.0205) (0.0207) (0.0209) (0.0206) (0.0209) (0.0201) (0.0202) (0.0200) Degree -0.0238 -0.0250 -0.0208 -0.0208 -0.0204 -0.0203 -0.0251 -0.0250 -0.0247 (0.0182) (0.0183) (0.0186) (0.0185) (0.0186) (0.0184) (0.0183) (0.0183) (0.0182) Unemployed -0.0497** -0.0479** -0.0190 -0.0182 -0.0191 -0.0182 0.0089 -0.0477** -0.0045 (0.0215) (0.0213) (0.0226) - (0.0229) (0.0226) (0.0229) (0.0329) (0.0212) (0.0360) Union -0.0147 -0.0141 -0.0081 -0.0080 -0.0083 -0.0083 -0.0137 -0.0146 -0.0144 (0.0104) (0.0107) (0.0107) (0.0107) (0.0107) (0.0107) (0.0107) (0.0108) (0.0108) Income 0.0374* 0.0325 0.0176 0.0170 0.0171 0.0163 0.0320 -0.0319 -0.0214 (0.0200) (0.0196) (0.0207) (0.0209) (0.0208) (0.0210) (0.0195) (0.0392) (0.0407) Day -0.0005 -0.0005 -0.0005 0.0001 -0.0007 -0.0001 -0.0003 -0.0014* -0.0013 (0.0006) (0.0006) (0.0006) (0.0010) (0.0006) (0.0010) (0.0006) (0.0008) (0.0008) PC PID 0.0223 0.0193 0.0195 -0.0151 -0.0173 0.0222 0.0218 -0.0074 (0.0141) (0.0146) (0.0146) (0.0274) (0.0277) (0.0141) (0.0140) (0.0277) No PID -0.0201 -0.0160 -0.0155 -0.0160 -0.0154 -0.0207 -0.0203 -0.0207 (0.0140) (0.0136) (0.0136) (0.0137) (0.0136) (0.0140) (0.0140) (0.0140) PEP 0.1559*** (0.0231) O.1939*** (0.0522) 0.1558*** (0.0231) 0.1984*** (0.0526) PEP*Day -0.0015 (0.0018) -0.0017 (0.0018) PC PID*Day 0.0014 (0.0011) 0.0016 (0.0011) 0.0012 (0.0011) Unemp.*Day -0.0024* -0.0018 (0.0012) (0.0014) (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0026* 0.0021 (0.0014) (0.0015) Constant 0.3585*** 0.3603*** 0.3014*** 0.2874*** 0.3079*** 0.2928*** 0.3559*** 0.3819*** 0.3803*** (0.0186) (0.0206) (0.0218) (0.0292) (0.0223) (0.0292) (0.0206) (0.0235) (0.0254) Observations 1767 1767 1767 1767 1767 1767 1767 1767 1767 R-squared 0.07 0.07 0.10 0.10 0.10 0.11 0.07 0.07 0.07 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.33, NEP Models, Low Sophistication Estimates, Canada 1997 (1) (2) (3) (4) (5) (6) (7) (8) (9) . Woman -0.0947*** -0.0948*** -0.0892*** -0.0902*** -0.0892*** -0.0902*** -0.0947*** -0.0943*** -0.0943*** (0.0220) (0.0219) (0.0224) (0.0221) (0.0224) (0.0221) (0.0220) (0.0217) (0.0218) > 55 yrs. -0.0000 -0.0094 -0.0006 -0.0015 -0.0006 -0.0015 -0.0097 -0.0098 -0.0101 (0.0290) (0.0281) (0.0282) (0.0284) (0.0282) (0.0284) (0.0281) (0.0281) (0.0281) Non-European -0.0222 -0.0299 -0.0388 -0.0398 -0.0392 -0.0401 -0.0296 -0.0293 -0.0301 (0.0481) (0.0476) (0.0468) (0.0465) (0.0463) (0.0460) (0.0478) (0.0476) (0.0471) French Speaker -0.0648 -0.0599 -0.0589 -0.0589 -0.0590 -0.0589 -0.0600 -0.0592 -0.0595 (0.0392) (0.0396) (0.0413) (0.0412) (0.0414) (0.0413) (0.0396) (0.0404) (0.0405) Catholic 0.0345 0.0268 0.0279 0.0288 0.0275 0.0285 0.0266 0.0265 0.0255 (0.0293) (0.0287) (0.0297) (0.0296) (0.0297) (0.0296) (0.0288) (0.0287) (0.0289) Non-religious 0.0243 0.0315 0.0390 0.0383 0.0390 0.0383 0.0313 0.0307 0.0307 (0.0283) (0.0297) (0.0301) (0.0303) (0.0301) (0.0304) (0.0296) (0.0294) (0.0294) West -0.0258 -0.0101 -0.0097 -0.0115 -0.0097 -0.0116 -0.0099 -0.0104 -0.0103 (0.0279) (0.0264) (0.0253) (0.0249) (0.0254) (0.0250) (0.0264) (0.0266) (0.0266) Quebec -0.0703* -0.0636 -0.0516 -0.0544 -0.0514 -0.0542 -0.0632 -0.0645 -0.0633 (0.0400) (0.0399) (0.0413) (0.0416) (0.0415) (0.0417) (0.0399) (0.0403) (0.0406) Atlantic -0.1517*** -0.1407*** -0.1297*** -0.1314*** -0.1300*** -0.1316*** -0.1398*** -0.1408*** -0.1407*** (0.0423) (0.0409) (0.0395) (0.0395) (0.0391) (0.0392) (0.0407) (0.0410) (0.0405) Degree 0.1025*** 0.1013*** 0.0964*** 0.0959*** 0.0963*** 0.0959*** 0.1014*** 0.1012*** 0.1012*** (0.0295) (0.0290) (0.0299) (0.0301) (0.0299) (0.0301) (0.0290) (0.0290) (0.0290) Unemployed -0.0945*** -0.1015*** -0.0664** -0.0675** -0.0664** -0.0674** -0.0631 -0.1013*** -0.0626 (0.0319) (0.0307) (0.0304) (0.0302) (0.0305) (0.0303) (0.0697) (0.0308) (0.0717) Union -0.0141 -0.0160 -0.0049 -0.0050 -0.0049 -0.0050 -0.0164 -0.0162 -0.0168 (0.0271) (0.0262) (0.0266) (0.0265) (0.0265) (0.0265) (0.0260) (0.0261) (0.0259) Income 0.1200** 0.1128** 0.0847* 0.0833* 0.0845* 0.0831* 0.1125** . 0.0842 0.0871 (0.0453) (0.0451) (0.0458) (0.0462) (0.0453) (0.0457) (0.0451) (0.0840) (0.0860) Day -0.0003 -0.0003 -0:0003 0.0016 -0.0004 0.0015 -0.0001 -0.0008 -0.0009 (0.0010) (0.0010) (0.0010) (0.0021) (0.0011) (0.0021) (0.0009) (0.0019) (0.0020) Liberal PID 0.0689** 0.0659** 0.0668** 0.0588 0.0614 0.0685** 0.0681*** 0.0492 (0.0256) (0.0248) (0.0249) (0.0481) (0.0480) (0.0257) (0.0249) (0.0501) No PID -0.0319 -0.0355 -0.0355 -0.0356 -0.0355 -0.0323 -0.0323 -0.0328 (0.0220) (0.0218) (0.0220) (0.0219) (0.0220) (0.0222) (0.0221) (0.0223) PEP 0.2431*** (0.0422) 0.3210*** (0.0841) 0.2428*** (0.0423) 0.3204*** (0.0837) PEP*Day -0.0042 (0.0042) -0.0042 (0.0042) Lib. PID*Day 0.0004 (0.0022) 0.0003 (0.0022) 0.0010 (0.0022) Unemp.*Day -0.0020 -0.0020 (0.0030) (0.0030) (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0015 (0.0038) 0.0013 (0.0038) Constant 0.5651*** 0.5518*** 0.4368*** 0.4039*** 0.4394*** 0.4060*** 0.5490*** 0.5634*** 0.5654*** (0.0401) (0.0381) (0.0453) (0.0560) (0.0441) (0.0534) (0.0377) (0.0474) (0.0487) Observations 1580 1580 1580 1580 1580 1580 1580 1580 1580 R-squared 0.08 0.09 0.12 0.12 0.12 0.12 0.09 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.34. NEP Models, Low Sophistication Estimates, Canada 2000 (1) (2) (3) (4) (5) (6) (7). (8) (9) Woman -0.0733*** -0.0733*** -0.0722*** -0.0722*** -0.0722*** -0.0723*** -0.0733*** -0.0733*** -0.0733*** (0.0235) (0.0229) (0.0210) (0.0210) (0.0210) (0.0210) (0.0229) (0.0229) (0.0228) > 55 yrs. 0.0475 0.0481 0.0500 0.0507 0.0491 0.0497 0.0482 0.0480 0.0470 (0.0307) (0.0310) (0.0300) (0.0301) (0.0306) (0.0307) (0.0312) (0.0310) (0.0317) Non-European 0.0285 0.0262 0.0270 0.0276 0.0271 0.0278 0.0263 0.0262 0.0264 (0.0370) (0.0380) (0.0366) (0.0367) (0.0368) (0.0368) (0.0380) (0.0380) (0.0382) French Speaker -0.0471 -0.0434 -0.0386 -0.0384 -0.0379 -0.0376 -0.0436 -0.0434 -0.0426 (0.0320) (0.0318) (0.0307) (0.0310) (0.0310) (0.0313) (0.0317) (0.0320) (0.0321) Catholic 0.0620* 0.0576 0.0514 0.0528 0.0511 0.0526 0.0579 0.0576 0.0574 (0.0340) (0.0343) (0.0331) (0.0318) (0.0333) (0.0320) (0.0343) (0.0346) (0.0347) Non-religious -0.0504 -0.0575 -0.0633 -0.0630 -0.0638 -0.0635 -0.0573 -0.0575 -0.0580 (0.0476) (0.0486) (0.0477) (0.0476) (0.0479) (0.0478) (0.0487) (0.0486) (0.0492) West -0.1561*** -0.1532*** -0.1528*** -0.1511*** -0.1534*** -0.1516*** -0.1529*** -0.1532*** -0.1537*** (0.0392) (0.0394) (0.0377) (0.0367) (0.0378) (0.0369) (0.0392) (0.0394) (0.0394) Quebec -0.0694* -0.0663* -0.0517 -0.0520 -0.0521 -0.0525 -0.0661* -0.0663* -0.0666* (0.0392) (0.0389) (0.0396) (0.0397) (0.0396) (0.0397) (0.0387) (0.0391) (0.0389) Atlantic -0.0934** -0.0938* -0.0882* -0.0874* -0.0875* -0.0867* -0.0937* -0.0938* -0.0928* (0.0457) (0.0466) (0.0473) (0.0475) (0.0467) (0.0469) (0.0465) (0.0466) (0.0457) Degree 0.0579 0.0583 0.0531 0.0529 0.0533 0.0530 0.0586 0.0581 0.0584 (0.0580) (0.0585) (0.0598) (0.0604) (0.0602) (0.0608) (0.0588) (0.0585) (0.0592) Unemployed 0.0009 -0.0001 0.0038 0.0033 0.0044 0.0038 0.0151 0.0000 0.0188 (0.0397) (0.0396) (0.0363) (0.0364) (0.0359) (0.0361) (0.1056) (0.0397) (0.1133) Union 0.0029 0.0051 0.0086 0.0080 0.0083 0.0077 0.0050 0.0051 0.0046 (0.0269) (0.0267) (0.0250) (0.0252) (0.0250) (0.0252) (0.0267) (0.0267) (0.0268) Income 0.0911 0.0909* 0.0564 0.0560 0.0563 0.0558 0.0912* 0.0949 0.0985 (0.0542) (0.0534) (0.0525) (0.0528) (0.0523) (0.0526) (0.0537) (0.1244) (0.1292) Day -0.0020 -0.0020 -0.0016 -0.0007 -0.0020 -0.0010 -0.0020 -0.0020 -0.0024 (0.0013) (0.0014) (0.0014) (0.0028) (0.0014) (0.0028) (0.0015) (0.0025) (0.0026) Liberal PID 0.0361 0.0389 0.0395 0.0105 0.0088 0.0360 0.0362 -0.0022 (0.0371) (0.0374) (0.0374) (0.0603) (0.0602) (0.0372) (0.0372) (0.0626) No PID 0.0337 0.0342 0.0344 0.0347 0.0350 0.0338 0.0337 0.0346 (0.0307) (0.0325) (0.0325) (0.0322) (0.0322) (0.0306) (0.0307) (0.0304) PEP 0.1885*** (0.0382) 0.2251** (0.0825) 0.1879*** (0.0385) 0.2275** (0.0837) PEP*Day -0.0019 (0.0041) -0.0020 (0.0041) Lib. PID*Day 0.0015 (0.0033) 0.0016 (0.0033) 0.0020 (0.0036) Unemp.*Day -0.0008 -0.0009 (0.0049) (0.0053) to (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day -0.0002 -0.0004 (0.0057) (0.0058) Constant 0.6302*** 0.6093*** 0.5105*** 0.4901*** 0.5189*** 0.4975*** 0.6081*** 0.6078*** 0.6161*** (0.0501) (0.0518) (0.0540) (0.0616) (0.0577) (0.0649) (0.0534) (0.0653) (0.0715) Observations 957 957 957 957 957 957 957 957 957 R-squared 0.08 0.08 0.12 0.12 0.12 0.12 0.08 0.08 0.08 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.35. NEP Models, Low Sophistication Estimates, Canada 2004 (1) (2) (3) (4) (5) (6) (7) (8) (9) Woman -0.1081*** -0.1073*** -0.1077*** -0.1075*** -0.1075*** -0.1072*** -0.1089*** -0.1075*** -0.1089*** (0.0171) (0.0166) (0.0164) (0.0164) (0.0164) (0.0164) (0.0165) (0.0167) (0.0166) > 55 yrs. 0.0145 0.0033 0.0174 0.0173 0.0172 0.0171 0.0040 0.0028 0.0036 (0.0193) (0.0185) (0.0185) (0.0185) (0.0184) (0.0184) (0.0183) (0.0187) (0.0185) Non-European 0.0305 0.0186 0.0189 0.0187 0.0187 0.0185 0.0233 0.0185 0.0230 (0.0393) (0.0391) (0.0407) (0.0408) (0.0406) (0.0407) (0.0374) (0.0391) (0.0373) French Speaker -0.0241 -0.0040 -0.0142 -0.0136 -0.0149 -0.0144 -0.0034 -0.0036 -0.0037 (0.0355) (0.0349) (0.0332) (0.0329) (0.0334) (0.0331) (0.0347) (0.0349) (0.0348) Catholic 0.0195 0.0088 0.0087 0.0091 0.0086 0.0090 0.0103 0.0087 0.0102 (0.0196) (0.0201) (0.0205) (0.0205) (0.0205) (0.0204) (0.0196) (0.0201) (0.0196) Non-religious 0.0045 0.0061 -0.0024 -0.0018 -0.0029 -0.0023 0.0069 0.0060 0.0066 (0.0255) (0.0267) (0.0250) (0.0249) (0.0252) (0.0251) (0.0260) (0.0267) (0.0263) West -0.0018 0.0079 0.0004 0.0004 0.0006 0.0006 0.0079 0.0079 0.0081 (0.0186) (0.0184) (0.0174) (0.0174) (0.0175) (0.0175) (0.0185) (0.0184) (0.0185) Quebec -0.0091 -0.0213 -0.0134 -0.0140 . -0.0124 -0.0129 . -0.0215 -0.0216 -0.0210 (0.0313) (0.0308) (0.0292) (0.0291) (0.0293) (0.0292) (0.0310) (0.0309) (0.0313) Atlantic -0.0312 -0.0381 -0.0449 -0.0446 -0.0453 -0.0451 -0.0382 -0.0381 -0.0385 (0.0287) (0.0297) (0.0284) (0.0284) (0.0284) (0.0284) (0.0300) (0.0297) (0.0300) Degree 0.0497** 0.0508** 0.0454* 0.0449* 0.0456* 0.0451* 0.0498** 0.0505** 0.0498** (0.0233) (0.0230) (0.0230) (0.0231) (0.0228) (0.0228) (0.0225) (0.0229) (0.0223) Unemployed -0.0845** -0.0786** -0.0584* -0.0600* -0.0574* -0.0590* 0.0912* -0.0791** 0.0899* (0.0324) (0.0314) (0.0321) (0.0319) (0.0322) (0.0320) (0.0475) (0.0315) (0.0469) Union -0.0163 -0.0130 -0.0161 -0.0162 -0.0158 -0.0159 -0.0129 -0.0131 -0.0127 (0.0198) (0.0198) (0.0206) (0.0206) (0.0205) (0.0205) (0.0197) (0.0197) (0.0196) Income 0.1180*** 0.1058*** 0.0883*** 0.0889*** .0.0883*** 0.0889*** 0.1069*** 0.0845** 0.0954** (0.0214) (0.0215) (0.0227) (0.0229) (0.0226) (0.0229) (0.0214) (0.0404) (0.0395) Day 0.0023** 0.0024** 0.0021* 0.0009 0.0024* 0.0012 0.0028*** 0.0020 0.0028** (0.0011) (0.0011) (0.0010) (0.0016) (0.0012) (0.0016) (0.0010) (0.0012) (0.0013) Liberal PID 0.1002*** 0.0887*** 0.0881*** 0.1109*** 0.1140*** 0.1012*** 0.1003*** 0.1165*** (0.0187) (0.0181) (0.0178) (0.0394) (0.0409) (0.0187) (0.0186) (0.0397) No PID -0.0159 -0.0126 -0.0127 -0.0125 -0.0125 -0.0159 -0.0157 -0.0157 (0.0190) (0.0185) (0.0185) (0.0187) (0.0187) (0.0189) (0.0190) (0.0191) PEP 0.1756*** (0.0273) 0.1260** (0.0597) 0.1760*** (0.0272) 0.1232* (0.0612) PEP*Day 0.0025 (0.0025) 0.0027 (0.0026) Lib. PID*Day -0.0011 (0.0017) -0.0013 (0.0018) -0.0008 (0.0017) Unemp.*Day -0.0092*** -0.0091*** (0.0032) (0.0031) (1) (2) (3) (4) (5) (6) (7) (8) (9) Income*Day 0.0011 0.0006 (0.0017) (0.0017) Constant 0.4042*** 0.3866*** 0.3232*** 0.3452*** 0.3162*** 0.3385*** 0.3771*** 0.3961*** 0.3776*** (0.0350) (0.0363) (0.0396) (0.0472) (0.0408) (0.0466) (0.0357) (0.0390) (0.0398) Observations 2386 2386 2386 2386 2386 2386 2386 2386 2386 R-squared 0.06 0.08 0.11 0.11 0.11 0.11 0.08 0.08 0.08 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.36. NEP Models, Low Sophistication Estimates, New Zealand 1996 (1) (2) (3) (4) (5) (6) Woman -0.0378** -0.0394** -0.0401** -0.0404** -0.0404** -0.0422** (0.0182) (0.0180) (0.0177) (0.0179) (0.0179) (0.0176) Age -0.0026*** -0.0027*** -0.0027*** -0.0027*** -0.0027*** -0.0027*** (0.0008) (0.0008) (0.0008) (0.0008) (0.0008) (0.0008) Homeowner -0.0289 -0.0340 -0.0341 -0.0354 -0.0336 -0.0350 (0.0275) (0.0264) (0.0265) (0.0261) (0.0262) (0.0259) Working Class -0.0662** -0.0547* -0.0547* -0.0555* -0.0554* -0.0561* (0.0312) (0.0297) (0.0299) (0.0296) (0.0297) (0.0299) Degree 0.0033 0.0003 0.0015 0.0009 0.0005 0.0026 (0.0192) (0.0190) (0.0191) (0.0190) (0.0194) (0.0196) Union -0.0104 -0.0038 -0.0054 -0.0032 -0.0033 -0.0045 (0.0213) (0.0212) (0.0214) (0.0213) (0.0212) (0.0215) Public Sector Employee 0.0292 0.0358 0.0354 0.0351 0.0353 0.0341 (0.0236) (0.0233) (0.0236) (0.0233) (0.0233) (0.0236) Unemployed -0.0152 -0.0109 -0.0108 0.1498* -0.0118 0.1351* (0.0648) (0.0629) (0.0634) (0.0763) (0.0615) (0.0778) Income 0.1034** 0.0943** 0.0951** 0.0966** 0.0070 0.0040 (0.0416) (0.0417) (0.0417) (0.0420) (0.0685) (0.0711) Day 0.0024*** 0.0027*** 0.0033*** 0.0029*** -0.0008 -0.0003 (0.0008) (0.0008) (0.0008) (0.0008) (0.0019) (0.0019) National PID 0.0882*** 0.1272*** 0.0886*** 0.0872*** 0.1318*** (0.0197) (0.0359) (0.0197) (0.0194) (0.0371) No PID 0.0068 0.0067 0.0067 0.0051 0.0048 (0.0209) (0.0210) (0.0209) (0.0210) (0.0212) National PID*Day -0.0022 (0.0016) -0.0026 (0.0017) Unemployed*Day -0.0067** (0.0033) -0.0061* (0.0033) Income* Day 0.0046* (0.0026) 0.0049* (0.0029) Constant 0.5463*** 0.5221*** 0.5125*** 0.5191*** 0.5912*** 0.5822*** (0.0422) (0.0399) (0.0384) (0.0397) (0.0611) (0.0601) Observations 948 942 942 942 942 942 R-squared 0.07 0.10 0.10 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.37. NEP Models, Low Sophistication Estimates, New Zealand 1999 (1) (2) (3) (4) (5) (6) Woman -0.0301** -0.0317** -0.0320** -0.0312** -0.0314** -0.0312** (0.0133) (0.0129) (0.0128) (0.0130) (0.0129) (0.0128) Age -0.0024*** -0.0024*** -0.0024*** -0.0024*** -0.0024*** -0.0024*** (0.0005) (0.0006) (0.0006) (0.0006) (0.0006) (0.0006) Maori -0.0821* -0.0736* -0.0738* -0.0734 -0.0720 -0.0716 (0.0443) (0.0433) (0.0430) (0.0436) (0.0436) (0.0437) Degree 0.0043 0.0038 0.0037 0.0056 0.0026 0.0041 (0.0214) (0.0208) (0.0207) (0.0212) (0.0214) (0.0218) Union 0.0077 0.0145 0.0144 0.0159 0.0155 0.0171 (0.0197) (0.0198) (0.0198) (0.0197) (0.0197) (0.0195) Public Sector Employee -0.0204 -0.0200 -0.0198 -0.0221* -0.0206* -0.0227* (0.0124) (0.0119) (0.0119) (0.0119) (0.0120) (0.0120) Manual Worker -0.0228 -0.0199 -0.0199 -0.0201 -0.0212 -0.0218 . (0.0283) (0.0283) (0.0283) (0.0283) (0.0277) (0.0276) Farmer 0.0378 0.0222 0.0223 0.0220 0.0215 0.0213 (0.0478) (0.0484) (0.0482) (0.0485) (0.0484) (0.0481) Unemployed 0.0291 0.0377 0.0373 0.1224*** 0.0376 0.1269*** (0.0242) (0.0247) (0.0247) (0.0368) (0.0248) (0.0395) Income 0.1410*** 0.1231*** 0.1224*** 0.1226*** 0.1711*** 0.1798*** (0.0324) (0.0324) (0.0324) (0.0323) (0.0541) (0.0564) Day 0.0027** 0.0026*** 0.0024** 0.0028*** 0.0043** 0.0045** (0.0010) (0.0010) (0.0011) (0.0009) (0.0018) (0.0019) National PID 0.0623** 0.0482 0.0621** 0.0625** 0.0441 (0.0236) (0.0420) (0.0236) (0.0236) (0.0427) No PID 0.0111 0.0116 0.0102 0.0106 0.0102 (0.0145) (0.0144) (0.0144) (0.0146) (0.0145) National PID*Day 0.0009 (0.0019) 0.0012 (0.0020) Unemployed*Day -0.0050** (0.0018) -0.0053** (0.0019) Income*Day -0.0030 (0.0023) -0.0036 (0.0024) Constant 0.4789*** 0.4682*** 0.4725*** 0.4654*** 0.4418*** 0.4389*** (0.0399) (0.0394) (0.0394) (0.0392) (0.0517) (0.0520) Observations 952 952 952 952 952 952 R-squared 0.09 0.10 0.10 0.10 0.10 0.10 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% O Table A2.38. NEP Models, Low Sophistication Estimates, New Zealand 2002 (1) (2) (3) (4) (5) (6) Age 0.0028*** 0.0025*** 0.0026*** 0.0025*** 0.0025*** 0.0026*** (0.0007) (0.0007) (0.0007) (0.0007) (0.0007) (0.0007) Woman -0.0170 -0.0174 -0.0182 -0.0174 -0.0204 -0.0211 (0.0140) (0.0140) (0.0139) (0.0141) (0.0139) (0.0137) Manual Worker -0.0452 -0.0437 -0.0442 -0.0437 -0.0382 -0.0391 (0.0429) (0.0427) (0.0420) (0.0427) (0.0408) (0.0404) Union 0.0144 0.0049 0.0051 0.0049 0.0061 0.0063 (0.0199) (0.0202) (0.0200) (0.0202) (0.0192) (0.0192) Unemployed -0.0029 -0.0130 -0.0102 -0.0096 -0.0073 0.0208 (0.0347) (0.0294) (0.0328) (0.0633) (0.0299) (0.0626) Income 0.0261 0.0347 0.0396 0.0348 0.1438* 0.1395* (0.0467) (0.0463) (0.0457) (0.0464) (0.0786) (0.0811) Day -0.0011 -0.0010 -0.0020* -o:ooio 0.0025* 6.0014 (0.0007) (0.0007) (0.0010) (0.0007) (0.0015) (0.0018) Labour PID 0.0719*** 0.0176 0.0719*** 0.0688*** 0.0221 (0.0229) (0.0414) (0.0229) (0.0217) (0.0405) No PID 0.0092 . 0.0101 0.0092 0.0083 0.0093 (0.0199) (0.0196) (0.0200) (0.0196) (0.0195) Labour PID*Day 0.0033* (0.0018) 0.0029 (0.0018) Unemployed*Day -0.0002 (0.0033) -0.0017 (0.0031) Income*Day -0.0066* (0.0035) -0.0060* (0.0036) Constant 0.5437*** 0.5272*** 0.5390*** 0.5271*** 0.4709*** 0.4850*** (0.0454) (0.0508) (0.0518) (0.0509) (0.0633) (0.0653) Observations 1013 1013 1013 1013 1013 1013 R-squared 0.06 0.08 0.08 0.08 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% to to Table A2.39. NEP Models, Low Sophistication Estimates, United Kingdom 2001 (1) (2) (3) (4) (5) (6) . (7) . (8) Age 0.0003 0.0003 0.0003 0.0003 0.0003 0.0003 0.0003 0.0003 (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) (0.0004) Woman -0.0243* -0.0181 -0.0238* -0.0238* -0.0239* -0.0239* -0.0181 -0.0183 (0.0137) (0.0130) (0.0127) (0.0127) (0.0128) (0.0128) (0.0130) (0.0131) Homeowner -0.0326** -0.0114 -0.0175 -0.0174 -0.0174 -0.0174 -0.0114 -0.0113 (0.0133) (0.0126) (0.0122) (0.0122) (0.0122) (0.0122) (0.0126) (0.0126) Southeast -0.0022 0.0104 0.0113 0.0112 0.0113 0.0112 0.0105 0.0104 (0.0204) (0.0202) (0.0193) (0.0193) (0.0194) (0.0194) (0.0203) (0.0203) Southwest -0.0298 -0.0004 -0.0046 -0.0043 -0.0049 -0.0046 -0.0004 -0.0008 (0.0256) (0.0253) (0.0246) (0.0250) (0.0245) (0.0249) (0.0252) (0.0251) Midlands 0.0046 -0.0006 0.0020 0.0023 0.0020 0.0023 -0.0007 -0.0007 (0.0203) (0.0205) (0.0209) (0.0211) (0.0210) (0.0211) (0.0205) (0.0206) North 0.0224 0.0086 0.0096 0.0098 0.0100 0.0101 0.0087 0.0091 (0.0209) (0.0210) (0.0202) (0.0202) (0.0203) (0.0203) (0.0212) (0.0213) Wales 0.0043 -0.0029 -0.0065 -0.0063 -0.0064 -0.0062 -0.0027 -0.0026 (0.0280) (0.0274) (0.0238) (0.0239) (0.0240) (0.0240) (0.0277) (0.0278) Scotland -0.0102 -0.0066 -0.0079 -0.0079 -0.0080 -0.0080 -0.0067 -0.0067 (0.0290) (0.0308) (0.0286) (0.0286) (0.0287) (0.0287) (0.0308) (0.0309) Working Class 0.0243 0.0081 0.0073 0.0072 0.0073 0.0072 0.0081 0.0081 (0.0147) (0.0135) (0.0131) (0.0132) (0.0132) (0.0132) (0.0136) (0.0137) Unemployed -0.0663** -0.0761*** -0.0678** -0.0680** -0.0676** -0.0678** -0.0829 -0.0802 (0.0245) (0.0248) (0.0276) (0.0275) (0.0276) (0.0275) (0.0510) (0.0492) Day -0.0007 -0.0010 -0.0013** -0.0018 -0.0016* -0.0020 -0.0010* -0.0014* (0.0008) (0.0006) (0.0006) (0.0015) (0.0008) (0.0016) (0.0006) (0.0008) Labour PID 0.1722*** 0.1461*** 0.1460*** 0.1334*** 0.1345*** 0.1722*** 0.1576*** (0.0107) (0.0111) (0.0111) (0.0256) (0.0252) (0.0107) (0.0249) No Maj. Pty. PID 0.0122 0.0123 0.0125 0.0122 0.0123 0.0122 0.0120 (0.0344) (0.0320) (0.0320) (0.0320) (0.0320) (0.0344) (0.0344) PEP 0.1943*** (0.0238) 0.1791*** (0.0484) 0.1940*** (0.0239) 0.1835*** (0.0474) PEP* Day 0.0010 (0.0028) 0.0007 (0.0028) Lab. PID*Day 0.0008 (0.0015) 0.0008 (0.0015) 0.0009 (0.0014) Unemp.*Day 0.0005 (0.0029) 0.0003 (0.0028) Constant 0.5729*** 0.4887*** 0.4091*** 0.4169*** 0.4144*** 0.4193*** 0.4891*** 0.4948*** (0.0326) (0.0289) (0.0323) (0.0393) (0.0340) (0.0402) (0.0292) (0.0305) Observations 1940 1916 1883 1883 1883 1883 1916 1916 R-squared 0.01 0.12 0.15 0.15 0.15 0.15 0.12 0.12 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% to to to Table A2.40. NEP Models, Low Sophistication Estimates, United States 2000 (1) (2) (3) (4) (5) (6) (7) (8) (9) Male 0.0502*** 0.0535*** 0.0498*** 0.0497*** 0.0497*** 0.0497*** 0.0535*** 0.0535*** 0.0535*** (0.0094) (0.0093) (0.0089) (0.0089) (0.0089) (0.0089) (0.0093) (0.0094) (0.0094) Black -0.0657*** -0.0748*** -0.0722*** -0.0724*** -0.0721*** -0.0724*** -0.0748*** -0.0749*** -0.0748*** (0.0153) (0.0154) (0.0150) (0.0150) (0.0149) (0.0150) (0.0153) (0.0153) (0.0153) Evangelical -0.0254** -0.0286*** -0.0328*** -0.0325*** -0.0325*** -0.0323*** -0.0286*** -0.0286*** -0.0284*** (0.0103) (0.0099) (0.0085) (0.0085) (0.0085) (0.0085) (0.0099) (0.0099) (0.0099) Union -0.0062 -0.0071 -0.0044 -0.0045 -0.0043 -0.0044 -0.0072 -0.0071 -0.0071 (0.0123) (0.0121) (0.0123) (0.0123) (0.0124) (0.0124) (0.0121) (0.0121) (0.0122) Unemployed -0.1001*** -0.0933*** -0.0511 -0.0513 -0.0508 -0.0509 -0.1069 -0.0932*** -0.1042 (0.0318) (0.0307) (0.0308) (0.0308) (0.0311) (0.0311) (0.0777) (0.0307) (0.0801) Income 0.2489*** 0.2450*** 0.0743*** 0.0750*** 0.0741*** 0.0748*** 0.2450*** 0.2583*** 0.2536*** (0.0219) (0.0222) (0.0195) (0.0194) (0.0195) (0.0194) (0.0222) . (0.0714) (0.0734) Day -0.0001 -0.0001 -0.0000 -0.0005 -0.0003 -0.0008 -0.0001 0.0001 -0.0002 (0.0003) (0.0003) (0.0003) (0.0007) (0.0003) (0.0007) (0.0003) (0.0007) (0.0008) Democrat PID 0.0174 0.0139 0.0141 -0.0207 -0.0203 0.0174 0.0174 -0.0135 (0.0108) (0.0095) (0.0096) (0.0168) (0.0170) (0.0108) (0.0107) (0.0226) No PID -0.0498*** -0.0374*** -0.0373*** -0.0377*** -0.0375*** -0.0498*** -0.0498*** -0.0500*** (0.0099) (0.0091) (0.0091) (0.0091) (0.0092) (0.0099) (0.0099) (0.0099) PEP 0.4184*** (0.0192) 0.3791*** (0.0535) 0.4185*** (0.0191) 0.3797*** (0.0536) PEP*Day 0.0010 (0.0012) 0.0010 (0.0012) Dem. PID*Day 0.0009** (0.0004) 0.0009** (0.0004) 0.0008 (0.0005) Unemp.*Day 0.0004 (0.0018) 0.0003 (0.0019) Income*Day -0.0003 (0.0016) -0.0002 • (0.0016) Constant 0.4373*** 0.4583*** 0.3136*** 0.3337*** 0.3240*** 0.3438*** 0.4585*** 0.4523*** 0.4639*** (0.0168) (0.0200) (0.0198) (0.0337) (0.0208) (0.0347) (0.0203) (0.0374) (0.0408) Observations 3609 3609 3609 3609 3609 3609 3609 3609 3609 R-squared 0.08 0.09 0.22 0.22 0.22 0.22 0.09 0.09 0.09 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% t o Table A2.41. Vote Models, General Estimates, Canada 1988 (1) (2) Woman -0.0719 -0.0748 (0.1476) (0.1471) > 55 yrs. 0.0396 0.0424 (0.1534) (0.1530) Non-European -0.1833 -0.1758 (0.2770) (0.2775) French Speaker 0.2048 0.1997 (0.2176) (0.2177) Catholic -0.0614 -0.0558 (0.1670) (0.1672) Non-religious -0.3360 -0.3144 (0.2170) (0.2180) West -0.0544 -0.0520 (0.1567) (0.1559) Quebec 0.3996* 0.4071* (0.2353) (0.2375) Atlantic 0.1225 0.1239 (0.1892) (0.1887) Degree 0.3248* 0.3249* (0.1736) (0.1729) Unemployed -0.6824** -0.6704** (0.2818) (0.2798) Union -0.1887 -0.1859 (0.1340) (0.1331) Income 0.7524*** 0.7437*** (0.2383) (0.2363) PC PID 3.4419*** 3.4434*** (0.1353) (0.1353) No PID 1.0623*** 1.0577*** (0.1636) (0.1623) NEP 2.1095*** 1.3213 (0.4188) (1.0624) Day -0.0007 -0.0188 (0.0043) (0.0208) NEP*Day 0.0299 (0.0327) Constant -4.1756*** -3.7085*** (0.3477) (0.6433) Observations 2803 2803 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.42. Vote Models, General Estimates, Canada 1993 (1) (2) Woman 0.3522** 0.3522** (0.1612) (0.1611) > 55 yrs. 0.1465 0.1460 (0.1840) (0.1838) Non-European 0.2004 0.2014 (0.2324) (0.2317) French Speaker 0.2366 0.2381 (0.2446) (0.2461) Catholic -0.2551 -0.2560 (0.2019) (0.2037) Non-religious 0.0480 0.0477 (0.2000) (0.2001) West -0.3667** -0.3660** (0.1821) (0.1808) Quebec -0.3023 -0.3012 (0.3122) (0.3121) Atlantic 0.3777 0.3798 (0.2352) (0.2320) Degree 0.2947* 0.2940* (0.1741) (0.1729) Unemployed -0.2605 -0.2610 (0.3492) (0.3485) Union -0.3388*** -0.3396*** (0.1263) (0.1260) Income 0.3497 0.3491 (0.2167) (0.2165) PC PID 3.2571*** 3.2570*** (0.1629) (0.1628) No PID 0.8552*** 0.8560*** (0.1963) (0.1971) NEP 0.7538** 0.6852 (0.3150) (0.5203) Day -0.0239*** -0.0250*** (0.0054) (0.0096) NEP*Day 0.0031 (0.0213) Constant -3.0083*** -2.9850*** (0.3323) (0.3592) Observations 3004 3004 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.43. Vote Models, General Estimates, Canada 1997 (1) (2) Woman -0.0654 -0.0654 (0.1442) (0.1451) > 55 yrs. -0.0407 -0.0407 (0.1473) (0.1475) Non-European 0.7706*** 0.7706*** (0.2467) (0.2453) French Speaker -0.2255 -0.2255 (0.2058) (0.2088) Catholic 0.3264** 0.3264** (0.1484) (0.1492) Non-religious 0.1012 0.1012 (0.2166) (0.2166) West -0.2334 -0.2334 (0.1927) (0.1923) Quebec -0.4823** -0.4823** (0.1903) (0.1907) Atlantic -0.5389** -0.5388** (0.2130) (0.2141) Degree -0.0649 -0.0649 (0.1404) (0.1404) Unemployed -0.0471 -0.0471 (0.3211) (0.3218) Union 0.0966 0.0966 (0.1473) (0.1473) Income -0.1444 -0.1444 (0.2401) (0.2400) Liberal PID 3.0065*** 3.0065*** (0.1471) (0.1469) No PID 0.7512*** 0.7512*** (0.1594). (0.1596) NEP 0.9151*** 0.9149*** (0.1994) (0.3194) Day -0.0031 -0.0031 (0.0051) (0.0117) NEP*Day 0.0000 (0.0158) Constant -2.9647*** -2.9646*** (0.3461) (0.3906) Observations 3071 3071 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.44. Vote Models, General Estimates, Canada 2000 (1) (2) Woman -0.1624 -0.1621 (0.1233) (0.1231) > 55 yrs. -0.0631 -0.0630 (0.1185) (0.1183) Non-European 0.1313 0.1309 (0.1754) (0.1751) French Speaker -0.2689* -0.2679* (0.1630) (0.1623) Catholic 0.0912 0.0906 (0.1378) (0.1369) Non-religious 0.0179 0.0189 (0.1759) (0.1753) West -0.3248* -0.3259* (0.1770) (0.1778) Quebec -0.5114*** -0.5125*** (0.1352) (0.1343) Atlantic -0.3823* -0.3850* (0.2165) (0.2178) Degree 0.2584 0.2571 (0.1617) (0.1611) Unemployed 0.1319 0.1311 (0.2348) (0.2339) Union 0.0039 0.0042 (0.1293) (0.1292) Income -0.1023 -0.1020 (0.1939) (0.1940) Liberal PID 3.7811*** 3.7815*** (0.2039) (0.2034) No PID 1.5015*** 1.5019*** (0.2296) (0.2292) NEP 0.6400*** 0.5742 (0.1574) (0.3751) Day -0.0136* -0.0158 (0.0073) (0.0116) NEP*Day 0.0033 (0.0150) Constant -2.9475*** -2.9019*** (0.4068) (0.4774) Observations 3026 3026 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.45. Vote Models, General Estimates, Canada 2004 (1) (2) Woman -0.0410 -0.0466 (0.1280) (0.1276) > 55 yrs. 0.2430* 0.2436* (0.1424) (0.1421) Non-European 0.7117*** 0.7136*** (0.1850) (0.1860) French Speaker -0.7403*** -0.7368*** (0.2144) (0.2136) Catholic 0.0348 0.0335 (0.1459) (0.1459) Non-religious 0.0714 0.0748 (0.1759) (0.1758) West -0.3141** -0.3147** (0.1355) (0.1365) Quebec 0.2375 0.2308 (0.2427) (0.2419) Atlantic 0.3195 0.3223 (0.2218) (0.2194) Degree 0.3628** 0.3583** (0.1431) (0.1432) Unemployed -1.1368** -1.1219** (0.5263) (0.5275) Union 0.0341 0.0365 (0.1291) (0.1291) Income 0.0182 0.0103 (0.1692) (0.1687) Liberal PID 3.3097*** 3.3149*** (0.1801) (0.1814) No PID 1.1422*** 1.1431*** (0.2118) (0.2117) NEP 0.5692*** 0.2441 (0.1761) (0.3382) Day 0.0007 -0.0082 (0.0079) (0.0126) NEP*Day 0.0169 (0.0155) Constant -3.7167*** -3.5466*** (0.2744) (0.3190) Observations 3519 3519 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.46. Vote Models, General Estimates, New Zealand 1996 (1) (2) Woman -0.1703 -0.1671 (0.1628) (0.1637) Age -0.0229*** -0.0229*** (0.0065) (0.0066) Homeowner 0.4918** 0.4929** (0.2446) (0.2443) Working Class -0.1895 -0.1979 (0.2093) (0.2096) Degree -0.1200 -0.1166 (0.2232) (0.2224) Union -0.6530*** -0.6477*** (0.1908) (0.1897) Public Sector -0.1815 -0.1856 (0.1686) (0.1692) Unemployed -2.9491*** -2.9640*** (1.0578) (1.0839) Income 0.7272** 0.7170** (0.3617) (0.3607) National PID 3.5497*** 3.5529*** (0.2717) (0.2717) No PID 1.6051*** 1.6062*** (0.2323) (0.2320) NEP 2.3709*** 2.0669*** (0.3088) (0.4298) Day -0.0113** -0.0204 (0.0055) (0.0167) NEP*Day 0.0168 (0.0280) Constant -3.2487*** -3.0899*** (0.5119) (0.5418) Observations 1328 1328 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.47. Vote Models, General Estimates, New Zealand 1999 (1) -(2) Woman 0.3688** 0.3834** (0.1882) (0.1871) Age -0.0080 -0.0086 (0.0057) (0.0057) Maori 0.2168 0.2106 (0.7505) (0.7748) Degree -0.4724* -0.4552* (0.2436) (0.2407) Union -0.6062** -0.6222** (0.2512) (0.2486) Public Sector 0.0457 0.0617 (0.1795) (0.1874) Manual Worker -0.2381 -0.2115 (0.1952) (0.1993) Farmer 0.4414 0.4494 (0.5546) (0.5807) Unemployed -0.4127 -0.3815 (0.5441) (0.5426) Income 1.2036*** 1.2020*** (0.3329) (0.3393) National PID 3.7564*** 3.7748*** (0.3841) (0.3815) No PID 1.9556*** 1.9708*** (0.3483) (0.3463) NEP 2.3371*** 0.7198 (0.4052) (0.8437) Day -0.0173* -0.0705*** (0.0098) (0.0233) NEP*Day 0.1038** (0.0457) Constant -4.4271*** -3.6345*** (0.5580) (0.6594) Observations 1180 1180 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.48. Vote Models, General Estimates, New Zealand 2002 CD (2) Age -0.0052 -0.0049 (0.0057) (0.0055) Woman -0.0310 -0.0233 (0.2050) (0.1979) Manual Worker -0.2341 -0.2489 (0.3824) (0.3592) Union 0.1318 0.1335 (0.2363) (0.2344) Unemployed -0.2644 -0.2622 (0.5207) (0.5273) Income -0.0399 -0.0521 (0.2783) (0.2651) Labour PID 4.5017*** 4.5142*** (0.2333) (0.2404) No PID 2.1501*** 2.1566*** (0.1977) (0.2008) NEP 1.0358* 1.6324* (0.6105) (0,9167) Day -0.0126 0.0089 (0.0093) (0.0492) NEP*Day -0.0327 (0.0662) Constant -2.6099*** -3.0239*** (0.4825) (0.7791) Observations 1473 1473 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.49. Vote Models, General Estimates, United Kingdom 2001 (1) (2) Age -0.0120*** -0.0120*** (0.0031) (0.0031) Woman 0.0102 0.0121 (0.0906) (0.0899) Homeowner -0.2359** -0.2335** (0.0944) (0.0943) Southeast -0.2034 -0.2096 (0.1736) (0.1729) Southwest -0.2023 -0.2031 (0.2056) (0.2056) Midlands -0.1993 -0.2053 (0.1854) (0.1841) North 0.0546 0.0509 (0.1789) (0.1784) Wales -0.3763* -0.3866* (0.2207) (0.2174) Scotland -0.1960 -0.2028 (0.2663) (0.2681) Working Class 0.2338*** 0.2311*** (0.0674) (0.0682) Unemployed -0.5651** -0.5526** (0.2860) (0.2813) Labour PID 3.2980*** 3.3006*** (0.0834) (0.0837) No Maj. Pty. PID 0.2084 0.2147 (0.2965) (0.2995) NEP 2.1314*** 2.5352*** (0.1970) (0.4391) Day -0.0017 0.0142 (0.0051) (0.0135) NEP*Day -0.0263 (0.0239) Constant -2.2373*** -2.4805*** (0.2583) (0.3500) Observations 4602 4602 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.50. Vote Models, General Estimates, United States 2000 (1) (2) Male -0.2808*** -0.2811*** (0.0369) (0.0369) Black 0.6898*** 0.6882*** (0.0841) (0.0843) Evangelical -0.7093*** -0.7099*** (0.0413) (0.0413) Union 0.3130*** 0.3128*** (0.0531) (0.0529) Unemployed 0.0677 0.0661 (0.1349) (0.1352) Income -0.1633** -0.1629** (0.0731) (0.0731) Democrat PID 3.5287*** 3.5309*** (0.0641) (0.0642) No PID 1.8158*** 1.8164*** (0.0511) (0.0512) NEP 1.0190*** 1.2190*** (0.0691) (0.1340) Day -0.0015 0.0022 (0.0011) (0.0026) NEP*Day -0.0063* (0.0038) Constant -2.4502*** -2.5700*** (0.0890) (0.1225) Observations 17382 17382 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% 234 Table A2.51, Vote Models, High Sophistication Estimates, Canada 1988 (!) (2) Woman -0.1432 -0.1477 (0.1929) (0.1930) > 55 yrs. 0.0751 0.0728 (0.1837) (0.1845) Non-European -0.2425 -0.2290 (0.2612) (0.2645) French Speaker -0.0059 -0.0024 (0.2977) (0.2965) Catholic -0.0154 -0.0085 (0.2129) (0.2129) Non-religious -0.1818 -0.1494 (0.2633) (0.2655) West -0.0879 -0.0883 (0.2123) (0.2123) Quebec 0.5541* 0.5565* (0.2952) (0.2955) Atlantic 0.1099 0.1131 (0.2724) (0.2714) Degree 0.2348 0.2326 (0.1885) (0.1880) Unemployed -0.6870** -0.6823** (0.3040) (0.3016) Union -0.0859 -0.0875 (0.2015) (0.2026) Income 0.9871*** 0.9778*** (0.3319) (0.3284) PC PID 3.4572*** 3.4657*** (0.1993) (0.1981) No PID 1.0579*** 1.0593*** (0.2328) (0.2330) NEP 2 7327*** 1.7055 (0.5104) (1.0511) Day 0.0010 -0.0232 (0.0065) (0.0263) NEP*Day 0.0385 (0.0383) Constant -4.7054*** -4.0729*** (0.5214) (0.7723) Observations 1524 1524 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.52. Vote Models, High Sophistication Estimates, Canada 1993 (1) (2) Woman 0.5112* 0.5123* (0.2771) (0.2785) > 55 yrs. -0.0855 -0.0801 (0.3501) (0.3469) Non-European 0.2896 0.2794 (0.2763) . (0.2743) French Speaker -0.1125 -0.1179 (0.3409) (0.3366) Catholic -0.3768 -0.3669 (0.3256) (0.3284) Non-religious -0.0356 -0.0368 (0.2966) (0.2932) West -0.5136* -0.5164** (0.2628) (0.2603) Quebec -0.1240 -0.1374 (0.3983) (0.3929) Atlantic 0.0977 0.0806 (0.3343) (0.3270) Degree 0.1576 0.1614 (0.2609) (0.2575) Unemployed -0.2324 -0.2240 (0.6122) (0.6184) Union -0.2368 -0.2335 (0.1926) (0.1924) Income 0.2162 0.2204 (0.3619) (0.3630) PC PID 3.3063*** 3.3111*** (0.2909) (0.2933) No PID 0.6677** 0.6614** (0.3351) (0.3364) NEP 1.5474*** 1.9443* (0.5930) (1.1238) Day -0.0359*** -0.0282 (0.0076) (0.0240) NEP* Day -0.0200 (0.0546) Constant -2.8785*** -3.0348*** (0.5033) (0.6803) Observations 1088 1088 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.53. Vote Models, High Sophistication Estimates, Canada 1997 (1) (2) Woman -0.2150 -0.2128 (0.1982) (0.1969) > 55 yrs. -0.1520 -0.1531 (0.1638) (0.1636) Non-European 0.7256** 0.7404** (0.3126) (0.3103) French Speaker -0.2342 -0.2270 (0.2469) (0.2544) Catholic 0.2504 0.2489 (0.2380) (0.2398) Non-religious -0.1528 -0.1547 (0.2647) (0.2657) West -0.0993 -0.0979 (0.2621) (0.2630) Quebec -0.5308* -0.5326* (0.2901) (0.2903) Atlantic -0.3999 -0.3972 (0.3263) (0.3277) Degree -0.2005 -0.2011 (0.1783) (0.1780) Unemployed 0.4778 0.4760 (0.5330) (0.5307) Union 0.1206 0.1193 (0.1791) (0.1802) Income -0.0345 -0.0355 (0.2708) (0.2694) Liberal PID 3.2244*** 3.2267*** (0.1941) (0.1955) No PID 1.1330*** 1.1342*** (0.2013) (0.2004) NEP 1.0698*** 0.8834 (0.3087) (0.6313) Day -0.0150 -0.0214 (0.0102) (0.0239) NEP*Day 0.0095 (0.0279) Constant -2.9990*** -2.8773*** (0.4739) (0.5972) Observations 1550 1550 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.54. Vote Models, High Sophistication Estimates, Canada 2000 (1) (2) Woman -0.0401 -0.0408 (0.1368) (0.1372) > 55 yrs. -0.1899 -0.1904 (0.1341) (0.1331) Non-European 0.0205 0.0186 (0.2146) (0.2152) French Speaker -0.3275* -0.3205* (0.1928) (0.1920) Catholic 0.0674 0.0645 (0.1718) (0.1693) Non-religious 0.1077 0.1095 (0.2188) (0.2195) West -0.4266** -0.4288** (0.2029) (0.2046) Quebec -0.4484** -0.4529** (0.1996) (0.2002) Atlantic -0.5217** -0.5301** (0.2199) (0.2290) Degree 0.2187 0.2148 (0.1848) (0.1819) Unemployed 0.2986 0.2956 (0.2073) (0.2062) Union -0.0182 -0.0153 (0.1623) (0.1613) Income -0.0623 -0.0625 (0.2339) (0.2337) Liberal PID 3.6720*** 3.6763*** (0.2427) (0.2390) No PID 1.5317*** 1.5325*** (0.2558) (0.2547) NEP 0.6219*** 0.3757 (0.2040) (0.5842) Day -0.0163* -0.0255 (0.0089) (0.0215) NEP*Day 0.0124 (0.0232) Constant -2.7881*** -2.6052*** (0.4580) (0.7059) Observations 2069 2069 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 % 238 Table A2.55. Vote Models, High Sophistication Estimates, Canada 2004 (1) (2) Woman 0.2098 0.2129 (0.2064) (0.2087) > 55 yrs. 0.1325 0.1345 (0.2499) (0.2479) Non-European 1.1762*** 1.1737*** (0.4432) (0.4420) French Speaker -1 2927*** -1.2907*** (0.4204) (0.4225) Catholic 0.3691 0.3674 (0.2244) (0.2254) Non-religious 0.4195 0.4186 (0.2596) (0.2600) West -0.3832 -0.3830 (0.2587) (0.2578) Quebec 0.2633 0.2646 (0.3413) (0.3399) Atlantic 0.5559* 0.5573* (0.3043) (0.3050) Degree 0.1208 0.1196 (0.2647) (0.2642) Unemployed 0.8491 0.8548 (0.9169) (0.9198) Union -0.3714* -0.3712* (0.2124) (0.2126) Income 0.2580 0.2654 (0.2410) (0.2378) Liberal PID 3.2316*** 3.2317*** (0.2116) (0.2118) No PID 0.9627*** 0.9677*** (0.2689) (0.2681) NEP 0.7762*** 0.9127 (0.2786) (0.6073) Day 0.0120 0.0167 (0.0125) (0.0283) NEP*Day -0.0074 (0.0290) Constant -4.0686*** -4.1590*** (0.3519) (0.5806) Observations 1132 1132 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1 % Table A2.56. Vote Models, High Sophistication Estimates, New Zealand 1996 (1) (2) Woman -0.2638 -0.3140 (0.3156) (0.3189) Age -0.0114 -0.0109 (0.0125) (0.0124) Homeowner -0.7494 -0.7626 (0.5620) (0.5696) Working Class -0.1028 -0.1140 (0.4569) (0.4676) Degree 0.0981 0.0548 (0.3880) (0.3862) Union -0.9542* -0.9863* (0.5200) (0.5080) Public Sector 0.2835 0.3332 (0.3474) (0.3480) Income 0.2097 0.3029 (0.7697) (0.7920) National PID 2.5794*** 2.6215*** (0.5200) (0.5379) No PID 1.3110*** 1.3499*** (0.4696) (0.4867) NEP 2.9030*** 4.3989*** (0.6685) (1.0419) Day 0.0099 0.0541** (0.0130) (0.0275) NEP*Day -0.0794* (0.0442) Constant -2.8783*** -3.7879*** (1.0042) (1.2637) Observations 328 328 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.57. Vote Models, High Sophistication Estimates, New Zealand 1999 (1) (2) Woman -0.3402 -0.2619 (0.5229) (0.5372) Age 0.0545 0.0426 (0.0343) (0.0326) Degree -1.2596 -1.2495 (0.8129) (0.8438) Union -0.6673 -0.7710 (1.0823) (1.0626) Public Sector -0.3898 -0.3291 (0.7144) (0.7541) Manual Worker -1.6208 -1.5625 (1.4447) (1.4032) Farmer 0.8079 0.9858 (0.7598) (0.7666) Unemployed 3.7232*** 3.6603*** (0.9988) (1.0218) Income 4.8087*** 4.7201** (1.8587) (1.9869) National PID 4.9294*** 5.0685*** (0.9577) (0.8998) No PID 1.4553 1.6191 (1.1145) (1.1431) NEP 1.2818 -1.1740 (1.4886) (2.1233) Day -0.0396 -0.1487*** (0.0362) (0.0574) NEP*Day 0.1846 (0.1167) Constant -9.9725*** -8.0101** (3.2945) (3.5692) Observations 206 206 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.58. Vote Models, High Sophistication Estimates, New Zealand 2002 (1) (2) Age 0.0061 0.0042 (0.0123) (0.0127) Woman 0.0784 0.0488 (0.3069) (0.3042) Manual Worker -0.8117 -0.8198 (0.7600) (0.7830) Union 0.1184 0.0868 (0.4329) (0.4353) Unemployed 0.6201 0.4961 (2.1092) (1.7834) Income -0.7409 -0.7934 (0.5762) (0.5685) Labour PID 3.6614*** 3.6999*** (0.5092) (0.5091) No PID 1.8883*** 1.8505*** (0.3209) (0.3119) NEP 2.0253** -0.2749 (0.9267) (1.5993) Day -0.0346** -0.1279** (0.0159) (0.0637) NEP*Day 0.1339 (0.0826) Constant -3.1049** -1.3526 (1.2988) (1.7853) Observations 362 362 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1' 242 Table A2.59. Vote Models, High Sophistication Estimates, United Kingdom 2001 (1) (2) Age -0.0090** -0.0090** (0.0041) (0.0041) Woman -0.0176 -0.0112 (0.1162) (0.1141) Homeowner -0.2446* -0.2439* (0.1268) (0.1280) Southeast -0.2303 -0.2437 (0.2194) (0.2188) Southwest -0.4174 -0.4078 (0.3180) (0.3189) Midlands -0.1259 -0.1412 (0.1998) (0.1968) North 0.2783 0.2726 (0.2032) (0.2031) Wales -0.0679 -0.0818 (0.3401) (0.3387) Scotland -0.0739 -0.0800 (0.3252) (0.3277) Working Class 0.2916*** 0.2865*** (0.0907) (0.0906) Unemployed -0.0452 -0.0206 (0.6266) (0.6196) Labour PID 3.4146*** 3.4195*** (0.1355) (0.1345) No Maj. Pty. PID 0.4035 0.4136 (0.4024) (0.4082) NEP 2.1856*** 2.7696*** (0.2866) (0.6312) Day -0.0119* 0.0119 (0.0064) (0.0202) NEP*Day -0.0385 (0.0348) Constant -2.3784*** -2 7342*** (0.3034) (0.4591) Observations 2679 2679 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.60. Vote Models, High Sophistication Estimates, United States 2000 (1) (2) Male -0.3870*** -0.3872*** (0.0946) (0.0945) Black 0.5927** 0.5908** (0.2421) (0.2417) Evangelical -0.9085*** -0.9102*** (0.1159) (0.1158) Union 0.3894*** 0.3879*** (0.1493) (0.1504) Unemployed -0.2271 -0.2346 (0.5037) (0.5082) Income -0.7206*** -0.7227*** (0.1703) (0.1713) Democrat PID 3.9595*** 3.9593*** (0.1723) (0.1722) No PID 2.1845*** 2.1849*** (0.1279) (0.1279) NEP 0.8387*** 0.6642 (0.1918) (0.5224) Day -0.0055** -0.0084 (0.0026) (0.0086) NEP*Day 0.0046 (0.0117) Constant -1.8277*** -1.7155*** (0.2149) (0.4099) Observations 3112 3112 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.61. Vote Models, Low Sophistication Estimates, Canada 1988 (1) (2) Woman 0.0726 0.0725 (0.2012) (0.2014) > 55 yrs. -0.0360 -0.0336 (0.2909) (0.2902) Non-European -0.1227 -0.1230 (0.4965) (0.4946) French Speaker 0.5322 0.5299 (0.3574) (0.3610) Catholic -0.1243 -0.1229 (0.2853) (0.2848) Non-religious -0.4617 -0.4589 (0.3415) (0.3419) West -0.0246 -0.0228 (0.2342) (0.2344) Quebec 0.1639 0.1664 (0.3789) (0.3848) Atlantic 0.1378 0.1371 (0.2825) (0.2823) Degree 0.3865 0.3865 (0.3366) (0.3365) Unemployed -0.7466* -0.7421* (0.4490) (0.4440) Union -0.3381 -0.3359 (0.2268) (0.2282) Income 0.4231 0.4201 (0.3253) (0.3253) PC PID 3.4315*** 3.4303*** (0.2551) (0.2532) No PID 1.0031*** 1.0008*** (0.2837) (0.2814) NEP 1.1917* 0.9959 (0.6344) (1.6745) Day -0.0027 -0.0071 (0.0076) (0.0301) NEP*Day 0.0077 (0.0492) Constant -3.5005*** -3.3903*** (0.5124) (0.9979) Observations 1273 1273 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.62. Vote Models, Low Sophistication Estimates, Canada 1993 (1) (2) Woman 0.1483 0.1460 (0.1909) (0.1907) > 55 yrs. 0.3840* 0.3854* (0.2142) (0.2133) Non-European 0.1959 0.2028 (0.2859) (0.2852) French Speaker 0.3461 0.3704 (0.2997) (0.3032) Catholic -0.2329 -0.2311 (0.2315) (0.2309) Non-religious 0.0344 0.0163 (0.3078) (0.3074) West -0.1969 -0.1817 (0.2340) (0.2349) Quebec -0.3752 -0.3790 (0.3755) (0.3762) Atlantic 0.5772* 0.6044* (0.3418) (0.3431) Degree 0.4955* 0.4907 (0.3007) (0.3022) Unemployed -0.3533 -0.3467 (0.5071) (0.5084) Union -0.3137* -0.3236* (0.1772) (0.1799) Income 0.7116** 0.7096** (0.3477) (0.3499) PC PID 3.0740*** 3.0728*** (0.2075) (0.2085) No PID 0.9205*** 0.9286*** (0.2396) (0.2411) NEP 0.2922 -0.6438 (0.3133) (0.5399) Day -0.0181*** -0.0305*** (0.0061) (0.0087) NEP*Day 0.0403* (0.0228) Constant -3.1072*** -2.8317*** (0.3598) (0.3436) Observations 1767 1767 Robust standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1% Table A2.63. Vote Models, Low Sophistication Estimates, Canada 1997 (1) (2) Woman 0.0500 0.0501 (0.1687) (0.1691) > 55 yrs. 0.1643 0.1643 (0.2138) (0.2138) Non-European 0.7947** 0.7957** (0.3383) (0.3405) French Speaker -0.3034 -0.3028 (0.2981) (0.2996) Catholic 0.4654** 0.4654** (0.1929) (0.1929) Non-religious 0.4801 0.4799 (0.2986) (0.2978) West -0.4186* -0.4186* (0.2508) (0.2508) Quebec -0.4271* -0.4272* (0.2324) (0.2323) Atlantic -0.7128** -0.7120** (0.3463) (0.3488) Degree 0.2810 0.2814 (0.2436) (0.2440) Unemployed -0.3345 -0.3339 (0.4145) (0.4147) Union 0.0860 0.0862 (0.2141) (0.2136) Income -0.1806 -0.1806 (0.3282) (0.3278) Liberal PID 2.8886*** 2.8885*** (0.2291) (0.2292) No PID 0.3790 0.3792 (0.-2658) (0.2656) NEP 0.8167*** 0.7940 (0.2958) (0.5600) Day 0.0103 0.0097 (0.0074) (0.0157) NEP*Day 0.0012 (0.0245) Constant -3.1314*** -3.1191*** (0.4726) (0.5485) Observations 1521 1521 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.64. Vote Models, Low Sophistication Estimates, Canada 2000 (1) (2) Woman -0.4796* -0.4848* (0.2671) (0.2706) > 55 yrs. 0.3713 0.3719 (0.2634) (0.2634) Non-European 0.3992 0.3990 (0.3142) (0.3168) French Speaker -0.0915 -0.0937 (0.3804) (0.3797) Catholic 0.2581 0.2598 (0.3217) (0.3209) Non-religious -0.1856 -0.1971 (0.4586) (0.4582) West -0.0663 -0.0545 (0.2439) (0.2439) Quebec -0.8493*** -0.8388*** (0.2661) (0.2732) Atlantic -0.1537 -0.1376 (0.4077) (0.4070) Degree 0.2297 0.2292 (0.3716) (0.3725) Unemployed -0.0176 -0.0108 (0.3799) (0.3812) Union 0.1062 0.1068 (0.2386) (0.2381) Income -0.2327 -0.2277 (0.3422) (0.3399) Liberal PID 4.2053*** 4.2112*** (0.3315) (0.3390) No PID 1.5479*** 1.5518*** (0.3658) (0.3672) NEP 0.6959** 0.9699 (0.3509) (1.0492) Day -0.0032 0.0043 (0.0098) (0.0252) NEP*Day -0.0139 (0.0465) Constant -3.4703*** -3.6304*** (0.6070) (0.8173) Observations 957 957 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.65. Vote Models, Low Sophistication Estimates, Canada 2004 (1) (2) Woman -0.1641 -0.1737 (0.1455) (0.1446) > 55 yrs. 0.2515 0.2550 (0.1595) (0.1593) Non-European 0.5736*** 0.5750*** (0.1873) (0.1890) French Speaker -0.4981* -0.4870* (0.2967) (0.2957) Catholic -0.1312 -0.1355 (0.1804) (0.1797) Non-religious -0.1070 -0.1049 (0.2005) (0.1996) West -0.2486 -0.2481 (0.1695) (0.1684) Quebec 0.2501 0.2351 (0.3113) (0.3112) Atlantic 0.2196 0.2242 (0.3307) (0.3275) Degree 0.5362*** 0.5208*** (0.1876) (0.1860) Unemployed -1.5205*** -1.4967*** (0.5431) (0.5519) Union 0.2425 0.2470 (0.1667) (0.1677) Income -0.1400 . -0.1425 (0.2392) (0.2399) Liberal PID 3.4545*** 3.4612*** (0.2476) (0.2497) No PID 1.2865*** 1.2885*** (0.2832) (0.2823) NEP 0.4139* -0.0244 (0.2311) (0.4416) Day -0.0042 -0.0149 (0.0074) (0.0146) NEP*Day 0.0224 (0.0211) Constant -3.6255*** -3.4189*** (0.3086) (0.3563) Observations 2386 2386 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% 249 Table A2.66. Vote Models, Low Sophistication Estimates, New Zealand 1996 (1) (2) Woman -0.1894 -0.1830 (0.1891) (0.1893) Age -0.0240*** -0.0235** (0.0093) (0.0093) Homeowner 0.7492** 0.7460** (0.3103) (0.3047) Working Class -0.3022 -0.3378 (0.2291) (0.2345) Degree -0.1393 -0.1379 (0.2939) (0.2943) Union -0.5415** -0.5330** (0.2188) (0.2213) Public Sector -0.3638 -0.3714* (0.2236) (0.2247) Unemployed -3.0144*** -3.0639*** (1.0062) (1.0731) Income 0.7367 0.7221 (0.5245) (0.5180) NationalPID 3.8391*** 3.8588*** (0.3303) (0.3314) No PID 1.6467*** 1.6550*** (0.2803) (0.2818) NEP 2.3645*** 1.3290** (0.3644) (0.6106) Day -0.0176*** -0.0481** (0.0055) (0.0201) NEP*Day 0.0567* (0.0335) Constant -3.2584*** -2.7429*** (0.6593) (0.6201) Observations 942 942 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% 250 Table A2.67. Vote Models, Low Sophistication Estimates, New Zealand 1999 (1) (2) Woman 0.3681* 0.3816* (0.2025) (0.2003) Age -0.0068 -0.0071 (0.0055) (0.0054) Maori 0.4248 0.4427 (0.7793) (0.7999) Degree -0.3406 -0.3313 (0.2728) (0.2694) Union -0.5990** -0.6144** (0.2586) (0.2584) Public Sector 0.1681 0.1784 (0.1994) (0.2071) Manual Worker -0.1735 -0.1506 (0.2130) (0.2184) Farmer 0.2687 0.2749 (0.6155) (0.6416) Unemployed -0.8396 -0.8148 (0.5941) (0.5917) Income 1.2272*** 1.2374*** (0.3289) (0.3358) National PID 3.5663*** 3.5610*** (0.4080) (0.4059) No PID 1.8541*** 1.8452*** (0.3783) (0.3740) . NEP 2.5188*** 1.1023 (0.3759) (0.6812) Day -0.0192** -0.0655*** (0.0093) (0.0195) NEP*Day 0.0913** (0.0394) Constant -4.4224*** -3.7334*** (0.5541) (0.5993) Observations 952 952 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% Table A2.68. Vote Models, Low Sophistication Estimates, New Zealand 2002 (1) (2) Age -0.0054 -0.0043 (0.0072) (0.0071) Woman 0.0148 0.0372 (0.2461) (0.2377) Manual Worker -0.1680 -0.2214 (0.4318) (0.3983) Union 0.1115 0.1207 (0.2705) (0.2676) Unemployed -0.5946 -0.5942 (0.4398) (0.4477) Income 0.2548 0.1962 (0.3682) (0.3401) Labour PID 4.8614*** 4.9060*** (0.2935) (0.3127) No PID 2.1599*** 2.1662*** (0.2675) (0.2702) NEP 0.9636 2.7103** (0.7779) (1.2007) Day -0.0082 0.0517 (0.0111) (0.0505) NEP*Day -0.0924 (0.0692) Constant -2.8180*** -4.0028*** (0.5957) (0.9079) Observations 1008 1008 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% 252 Table A2.69. Vote Models, Low Sophistication Estimates, United Kingdom 2001 (1) (2) Age -0.0161*** -0.0162*** (0.0046) (0.0046) Woman 0.0562 0.0561 (0.1347) (0.1347) Homeowner -0.2384 -0.2387 (0.1504) (0.1498) Southeast -0.2080 -0.2080 (0.2688) (0.2688) Southwest -0.0092 -0.0087 (0.3598) (0.3602) Midlands -0.3285 -0.3285 (0.3080) (0.3081) North -0.2684 -0.2683 (0.3139) (0.3139) Wales -0.7174** -0.7170** (0.3174) (0.3183) Scotland -0.4008 -0.4006 (0.4148) (0.4148) Working Class 0.1936 0.1937 (0.1269) (0.1280) Unemployed -0.6664** -0.6670** (0.3334) (0.3350) Labour PID 3.2249*** 3.2249*** (0.1380) (0.1380) No Maj.Pty. PID 0.0555 0.0555 (0.4292) (0.4294) NEP 2.0345*** 2.0112*** (0.2478) (0.5108) Day 0.0107 0.0099 (0.0070) (0.0172) NEP*Day 0.0015 (0.0280) Constant -2.0571*** -2.0433*** (0.4488) (0.5199) Observations 1916 1916 Robust standard errors in parentheses significant at 10%; ** significant at 5%; *** significant at 1% Table A2.70. Vote Models, Low Sophistication Estimates, United States 2000 (1) (2) Male -0.1927** -0.1929** (0.0966) (0.0966) Black 0.7622*** 0.7609*** (0.1543) (0.1553) Evangelical -0.6112*** -0.6122*** (0.0805) (0.0806) Union 0.3830*** 0.3826*** (0.1088) (0.1088) Unemployed -0.0184 -0.0178 (0.2536) (0.2540) Income -0.1460 -0.1463 (0.1771) (0.1773) Democrat PID 3.3697*** 3.3703*** (0.1530) (0.1534) No PID 1.6216*** 1.6213*** (0.1231) (0.1232) NEP 0.8431*** 0.9616** (0.1445) (0.4497) Day -0.0083*** -0.0066 (0.0031) (0.0059) NEP*Day -0.0031 (0.0103) Constant -2.1991*** -2.2649*** (0.1789) (0.2817) Observations 3609 3609 Robust standard errors in parentheses * significant at 10%; ** significant at 5%; *** significant at 1% 254 APPENDIX III: MEASURING POLITICAL SOPHISTICATION Proper measurement of political sophistication is crucial to most of the analysis in this dissertation. The conventional wisdom is that direct measures of general, factual political knowledge work best for this purpose (Price and Zaller 1993; Delli Carpini and Keeter 1996). Ideally, then, each of the ten surveys examined would include a similar battery of knowledge items. Alas, only three of the surveys (CES 1997, 2000 and 2004) include standard factual knowledge batteries, and even these may not be entirely comparable. Two other surveys include highly plausible surrogates for the standard measures: the NAES 2000 includes items tapping knowledge of candidate policy positions and the CES 1993 offers interviewer ratings of knowledge levels. In the five remaining surveys, however, sophistication levels must be measured more indirectly by combining measures of general political interest and media attention. A l l this variation in measurement poses obvious challenges for comparability. This appendix describes the construction of the political sophistication variables employed in the dissertation. General theoretical and operational principles are discussed first. This is followed by a comparative analysis of the ten variables. Key here is a performance analysis of each variable using indicators motivated by Delli Carpini and Keeter (1996). The aim of this analysis is to get a handle on the issue of comparability. The verdict here hinges partly on assumption; even so, it is clear that the various measures of political sophistication are at least roughly comparable. 255 General Principles As noted above, measures of general, factual political knowledge are regarded as the best indicators of cognitive heterogeneity in the electorate, at least in the context of survey research. This is so whether the target is actual 'volume' of political knowledge, level of politico-cognitive sophistication, or receptivity to political communications (Price and Zaller 1993; Delli Carpini and Keeter 1996; but see Luskin 1987, 1991). Thus, wherever possible, objective or subjective measures of factual political knowledge are utilized in this dissertation. Where such measures are unavailable, measures of closely related concepts must be substituted. The best available substitute for a direct knowledge measure is an indicator of general political interest (henceforth, GPI). The relationship between the two variables is strong and reciprocal. Luskin (1990), for instance, in his analysis of the determinants of political sophistication, finds that interest drives the political knowledge acquisition that supports political sophistication, and that political sophistication, in its turn, enhances political interest. Furthermore, in the three election studies examined here for which both direct, general political knowledge and GPI measures are available, GPI has powerful direct effects on knowledge levels, typically exceeding the impact of media attention and education by a significant margin (analysis unreported). Where possible, GPI indicators are combined with measures of attention to the print media. Luskin (1990) argues that attention to newspapers is the best measure of political information exposure. Furthermore, in the three surveys for which both knowledge and media attention variables are available, the effects of newspaper readership on knowledge generally eclipse those for attentiveness to television or radio 256 news (analysis unreported). Combining newspaper attention and GPI, thus, promises to enhances the validity and reliability of political sophistication variables where direct knowledge measures are unavailable. Whether the underlying measures are single variables or additive indexes, composed of knowledge items or measures of interest and media attention, all political sophistication variables are divided at their midpoints to form dichotomies. The aim is to facilitate easy comparison of psychological processes across sophistication levels. The first step is to scale the variables to range across the 0,1 interval. The 'high sophistication' category, then, consists of those respondents whose score on their respective index is strictly greater than 0.5; the 'low sophistication' category, accordingly, consists of respondents who are scored at 0.5 or lower. The uniform coding rule avoids potential arbitrariness in operationalizing sophistication thresholds across the various studies and also produces, happily, reasonably well performing measures (discussed below). It should also be noted that, where possible, campaign period (or pre-electoral) measures are favoured over post-electoral ones. The practice maximizes the number of observations for analysis. One risk here concerns the possibility that campaign period measures of knowledge and interest may confound their chronic component—what is of interest here—with their dynamic, campaign-induced component. The conflation could have the effect of systematic measurement error and, consequently, shrink estimated effects (raising the likelihood of Type II errors).1 Fortunately, there is strong evidence 1 The logic here is as follows: If the measure incorrectly assigns those low on political sophistication to the high sophistication category, because some respondents may report higher levels of chronic political interest and media attention inside than outside the campaign period, campaign effects estimates within 257 that knowledge and GPI measures are largely exogenous to the campaign across the elections examined here.2 The Measures: Construction Table A3.1 summarizes the components of each measure and reports relevant performance statistics. Consider first the details of variable construction. As noted above, three of the election surveys contain standard political knowledge batteries—those for Canada after 1993. Each battery consists of four items. In each of the three years, respondents are asked to name the Federal Minister of Finance and the premier of their home province. The remaining questions vary from year to year, but in all cases except one the questions focus on prominent political figures from Canada or elsewhere (question wordings below). In any case, for each year, the number of correct responses to the four items was summed and then transformed into a dichotomy, as described above. The closest approximation of the standard battery elsewhere in these data is for the United States, 2000. The NAES 2000 queries respondents on the policy positions of the major presidential candidates in that year. The battery consists of forty-one questions in total, although only a subset of respondents was asked each question. Most questions were asked only of random half-samples and not all questions appear for the full length of the general election period. Another constraint on the choice of questions is sophistication groups will be compressed. This is so whether campaign effects are confined to high or low sophistication respondents. 2 The inference rests on OLS models of the respective measures (results unreported). Regressing knowledge measures on day of campaign for the five elections concerned reveals insignificant movement across the campaign in three cases (Canada 1997, 2000; US 2000) and very moderate, negative movement in two others (Canada 1993, 2004). Regressing GPI measures on day of campaign for the two remaining elections employing pre-electoral measures leads to similar conclusions: very moderate, positive movement in one case (Canada 1988) and insignificant movement in the other (UK 2001). 3 These measures have been used to tap political knowledge elsewhere, and with some success; see Kenski (2003). 258 the fact that substantial 'learning' in some policy areas seems to have occurred over the campaign period—that is, the proportion of correct responses grew (and in a few cases shrank) over the campaign (analysis unreported). Including such items in an index of political sophistication would, thus, raise the spectre of measurement error, as described above; all such items were, accordingly, excluded from the analysis. Taking account of these various constraints, two sets of overlapping questions covering most of the fall campaign were identified for this analysis. The major distinction between the two sets of items is in terms of content validity4, and on these grounds a suitable knowledge scale was created (precise question wordings below). As above, the number of correct responses on these items was summed and the resulting index was transformed into a dichotomy.5 Across the remaining surveys, the best measure of political sophistication is the interviewer rating of respondent knowledge in the Canadian Election Study, 1993. In that survey, at the conclusion of each interview, interviewers recorded their perception of the respondent's level of political knowledge into one of five levels: very high, fairly high, average, fairly low, very low. Interviewers could also indicate that they did not know how to rate the respondent's knowledge level. 6 Measures like these have been 4 Specifically, one set of items focused strictly on 'moral' issues (the death penalty, gays in the military, soft money), while the other addressed a broader range of moral, social and economic concerns (child tax deductions, social security spending, prescription drug coverage for seniors, universal health care for children, tax credits for health care expenses, handgun licensing). As the aim is to index general political knowledge, the latter set of items is more suitable on its face. 5 Note that, owing to the fact that items were asked only of random halves of the Annenberg sampling frame, analyses conditioning on political sophistication cut the sample size for estimations for the US 2000 roughly in half. 6 A l l but about 5 percent of respondents were rated on the measure. The modal rating is 'average'—over 37 percent of cases fall into this category.—and the distribution of the measure is fairly normal. 259 found suitable in other contexts (Luskin 1991; Johnston et al. 1996) and the measure performs well here (see below). In analysis of the five other elections, political sophistication is measured with items tapping general political interest and attention to the print media, either alone or in combination. For Canada 1988, a simple additive index was created from GPI and newspaper attentiveness measures. Similar indices were created for New Zealand 1996 and 2002, with one notable difference owing to the measurement of GPI in these surveys. In all three of the New Zealand studies, the measure of general political interest took the following form: Generally speaking, how much interest do you usually have in what's going on in politics? Are you very interested, fairly interested, slightly interested or not at all interested? The problem with this measure concerns the two middle response categories, indicating 'fair' and 'slight' interest in politics. In short, there would seem to be a certain semantic asymmetry in these categories, such that the distribution of responses on this measure is somewhat 'top-heavy.' The argument is this: given the absence of an explicit middle category, respondents desiring to express a middle response must sort themselves into either of the two central categories. Were the two categories of 'fairly interested' and 'slightly interested' equally distant, in semantic terms, from some theoretical 'middle interest' point, we would expect the distribution of middle responses across these categories to be essentially random (Tourangeau, Rips and Rasinski 2000). It seems plausible, however, that most respondents would not see the two categories this way and that, in fact, 'slight' interest would be perceived as more distant from the middle than 'fair' interest. The inference rests on more than the intrinsic meaning of the two 260 modifiers; the distribution of GPI across the surveys supports this view. Most significantly, in the three surveys in which the above question wording is used (NZES 1996-2002), the modal response category is 'fairly interested,' attracting at least 50 percent of responses in every case. Furthermore, the 'fairly' interested outnumber the 'slightly' interested by at least 2:1 in these surveys. In four other surveys (CES 1997-2004, BES 2001), however, where GPI is measured on a more semantically continuous 0-10 scale, the modal response is 5 in every case, and the overall distributions are approximately normal with a modest positive skew. The implication is that the NZES items are positively biased. To address this potentially serious question wording problem, the GPI measures in the three New Zealand surveys are simply treated as dichotomies, where those who rate themselves as 'very interested' in politics score 1 and all others score 0. The coding decision represents a kind of 'bet' on the distribution of measurement error across different constructions of the variable. Specifically, the coding gambles that, among those in the fairly interested category, more are 'truly' only moderately interested in politics than are 'truly' very interested in politics. The gamble is supported by the above discussion of the response distributions on the various GPI measures and by analyses of the performance (see below) of different codings of these items.7 Once dichotomized, as noted above, in two cases (NZES 1996, 2002) these GPI items were used to form additive indexes with measures of print media attention. For o New Zealand 1999, due to data limitations , it was not possible to create such an index— 7 In general, use of the dichotomized GPI measure produces better performing political sophistication indicators (analysis unreported). 8 Coding errors in the original data set make the use of the media attention items problematic. 261 in this case, the GPI measure alone is used to index political sophistication. The GPI item stands alone in one other case: United Kingdom, 2001. Attention to print media in that election is measured with a simple binary measure ('Do you regularly read one or more daily morning newspapers? Yes/No') that is, on its face, too crude to capture important variation in media attentiveness (roughly 65 percent answer 'yes'). Including the item in the measure of political sophistication, furthermore, substantially diminishes the performance of the measure (analysis unreported). The Measures: Comparison As noted above, along with details of variable construction, Table A3.1 reports a series of performance statistics. These are motivated by Delli Carpini and Keeter's (1996) analysis of a wide range of factual political knowledge items. The basic logic of their analysis is to compare measures of political knowledge in terms of (a) their ability to discriminate across levels of general political knowledge and (b) their level of difficulty. Three statistics are crucial to such an analysis. First is simply the variable's mean, which, for a binary factual knowledge test item, reflects the proportion ip) of the sample that answers the item correctly. The second statistic is what they term the 'discrimination parameter' (Disc). This parameter derives from a logistic regression of the test item concerned on some indicator of latent ability.9 The coefficient on this indicator of ability is the discrimination parameter. The intercept from this regression model is the third statistic in the performance analysis—the 'difficulty parameter' 9 In their analysis, latent ability is proxied by a general political knowledge index. 262 (Diff.).10 Together, these statistics offer a useful basis on which to compare indicators of political knowledge across surveys, providing comparable measures of latent ability can be found. Of course, if a proper measure of latent ability were available in these data, that indicator would already be standing in for political sophistication in the analysis. Even so, by using a proxy for ability, we might hope to approximate Delli Carpini and Keeter's approach and, in so doing, address the comparability of the political sophistication measures somewhat rigorously. The most readily available such proxy in these data is the respondent's level of education. Directly comparable measures are present in all the surveys save for one (BES 2001), and even there a reasonable substitute is available. In every case, the variable is dichotomized, comparing degree-holders to all others.11 Regressing the political sophistication variable on this dichotomy for each election yields the set of performance statistics, p, Disc, and Diff., reported in Table A3.1. Consider first the distribution of p. Four measures yield values close to 0.5, meaning that the low and high sophistication categories are of roughly equal size in these samples (Canada 1988, 1997; U K 2001; US 2000). Five other measures would seem to be more difficult tests of political sophistication —at least two-thirds of their respective samples fall into the low sophistication category (Canada 1993, 2004; New Zealand 1996-2002). One test of political sophistication turns out to be relatively easy—in this case roughly two-thirds fall into the high sophistication category (Canada 2000). Diff. 10 Diff. and p are obviously directly related, except that p reflects both the intrinsic difficulty of the test item (Diff.) and the impact of latent ability on response to the item (Disc.) multiplied by the distribution of ability in the population. " The BES item does not query respondent's level of education; rather, it asks, 'At what age did you or will you complete your full-time education?' The top-most response category, '21 or over,' should in most cases indicate those holding at least undergraduate university credentials. 263 conveys much the same information, suggesting that most of the variability in p is driven by the intrinsic 'difficulty' of the measures, rather than by cross-national educational differences or the discriminating power of the measures. Impressionistically, the distribution of Disc, seems a good deal less variable. Seven of the measures produce values relatively close to 1. Two other measures are a little less discriminating by this standard (New Zealand 1999, 2002) and one is substantially more so (Canada 2000). Still, all the measures clearly discriminate between degree-holders and others, suggesting that some common dimension of politico-cognitive acumen is being tapped. What does all this imply for the comparability of the measures? The implications are subtle. Again, all the measures are linked in sensible ways to education, even if the strength of the link varies. This finding augurs well for comparability. But the 'difficulty' of the measures varies significantly, which means that the proportion of low sophistication respondents varies significantly across surveys. If the measures were perfectly conceptually equivalent, and if there were no significant cross-national variation in the distribution of underlying ability, the proportions should be roughly equal. But the measures clearly are not perfectly equivalent. For one thing, some are likely to be weaker predictors of general political knowledge than others—those relying on interest and attention rather than factual knowledge measures, for example. Furthermore, some of the variables are likely to incorporate more measurement error—recall the problematic response categories in the GPI measures for New Zealand. As a result, equivalent difficulty levels do not mean equivalent measures in this context. Indeed, efforts to equalize difficulty levels across the measures in many cases reduces their discriminating 264 power (analysis unreported), at the same time as it adds a certain arbitrariness to the analysis. Overall, then, an unknown degree of heterogeneity in the measurement of political sophistication is inevitable. It is clear that the measures are anchored by some common core of political knowledge and/or cognitive ability, as indexed by their relationship with education. Even so, the variables hook into this common concept differentially. This counsels caution in interpreting the models in this dissertation that condition on political sophistication and in generalizing the conclusions based on these results. At the same time, however, these measurement challenges make the appearance of common patterns across these elections more impressive; that is, assuming the measurement challenges take the form of random (as opposed to systematic) measurement error, common patterns in the data would presumably be even more striking if the measurement of political sophistication were more exacting. 265 Table A3.1. Political Sophistication Variables: Components and Performance Statistics Survey Components Mean (P) Disc. Dijf. CES 88 Pre-electoral GPI and NP measures 0.53 1.07 -0.02 CES 93 Pre-electoral interviewer knowledge rating 0.35 1.28 -0.87 CES 97 Pre-electoral factual knowledge measures 0.48 1.11 -0.30 CES 00 Pre-electoral factual knowledge measures 0.67 1.64 0.42 CES 04 Pre-electoral factual knowledge measures 0.30 1.00 -1.15 NZES 96 Post-electoral GPI and NP measures 0.21 0.95 -1.50 NZES 99 Post-electoral GPI measure 0.17 0.53 -1.67 NZES 02 Post-electoral GPI and NP measures 0.26 0.61 -1.23 BES01 Pre-electoral GPI measure 0.56 0.74 0.11 NAES 00 Pre-electoral candidate policy position knowledge measures 0.45 0.88 -0.50 Note: GPI: General political interest; NP: Attention to newspapers. 

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