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Policy Responsiveness and Electoral Incentives: A (Re)assessment

Abstract

Competitive democratic theory predicts that electoral factors enhance policy makers' responsiveness to public opinion. Yet findings on the effects of electoral incentives on policy responsiveness point in different directions and comparative research remains limited, lacking of a systematic evaluation. We draw on previous work, expand the range of electoral incentives, and re-assess their role in influencing policy responsiveness by using spending preferences. We provide extensive tests of an Electoral Vulnerability Hypothesis and an Electoral Proximity Hypothesis. Contra competitive democratic theory, time-series analysis from Canada, the United Kingdom and the United States in twenty policy domains and nine different indicators for electoral incentives finds limited support for these hypotheses. Our findings have implications for democracy and question the importance of electoral pressures in explaining policy responsiveness.

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Fig. 1

Notes

  1. This finding is backed up by consistent cross-country evidence on policy agendas that policy makers’ attention follows or is congruent with public issue priorities (Jones and Baumgartner 2004; Jennings and John 2009; Bonafont and Palau 2011; John et al. 2011; Lindeboom 2012; Bevan and Jennings 2014; Visconti 2018).

  2. However, note that re-election is not the only goal that parties would follow (Strøm 1990) and that governing parties have intrinsic preferences over the policies they enact (see, e.g., Wittman 1977, 1983).

  3. Soroka and Wlezien (2010, p. 139) provided a basic test for the hypothesis on social domains combined and found limited evidence of a marginality effect only in the United States (the interaction between public preferences and vote margin was statistically significant only at p ≤ 0.10), but not in the United Kingdom and Canada.

  4. Note that, in the United States, the impact of electoral pressures on policy responsiveness might be conditional on whether the Presidential party holds a majority in Congress. It might be the case that electoral incentives have a greater impact on policy responsiveness in cases of unified than divided government, for the President would have freer hands to follow what the public wants and the Congressional party may share the incentives of a president to be responsive to high salience public concerns (see Coleman 1999; Green and Jennings 2017). Unfortunately, our N is too small for fully testing this possibility empirically.

  5. Note that, although less relevant to us, a great deal of work focuses on US legislators’ roll call behaviour and, in comparison with the presidential literature, finds wide evidence that legislators are more responsive to public opinion in the year they face re-election.

  6. Data on Canada are downloaded from Soroka and Wlezien’s “Degrees of Democracy: Politics, Public Opinion and Policy” Canadian data set available at: http://www.degreesofdemocracy.net/data.html. Data on the United Kingdom and the United States are downloaded from the Replication data for the Jennings and Wlezien (2015) article published in Political Science Research and Methods available at: https://dataverse.harvard.edu/dataset.xhtml?persistentId=doi:10.7910/DVN/27496. Due to some missing values in the UK and US preferences, we follow Jennings and Wlezien (2015) and use interpolated data in our analyses.

  7. Of course other measures exist, but they are either about institutional vulnerability or based on aggregate electoral data such as indices of electoral competitiveness, the closeness of electoral result, and the frequency of turnover (Schlesinger 1955, 1960; Ranney 1965; Stern 1972; Meltz 1973; Elkins 1974; Ferejohn 1977; Patterson and Caldeira 1984; Endersby et al. 2002; Grofman and Selb 2009; Blais and Lago 2009; André et al. 2014; Immergut and Abou-Chadi 2014; Abou-Chadi and Orlowski 2016). These kinds of measures are problematic when we want to study government responsiveness, for at least three reasons. First, we simply are not interested in institutional vulnerability. Second, responsiveness occurs not at election time but between elections, therefore using measures based on election data would be problematic if not misleading. Third, such measures are time invariant and artificially static for the whole election cycle, they are US-specific, measured at the district level and not at the national level, or designed for other purposes. It is much better, both from a validity and degrees of freedom/variability perspective, to measure potential vulnerability with survey estimates for each year, rather than using the single value of the posterior elections for all the 3–5 years prior to the elections. Note that using measures based on voter’s propensity to vote (Kroh et al. 2007; Tillie 1995; van der Eijk and Oppenhuis 1991) would not solve our issue since such data come from pre-election surveys and hence not available at least on a yearly basis.

  8. Vote intentions data for Canada come from Environics, data for the United Kingdom come from different polls available in Wlezien et al. (2013) and Green and Jennings (2012), and data for the United States come, again, from different polls available in Jennings and Wlezien (2016).

  9. Being the United States a case of presidentialism with a pure two-party system, the formateur argument is clearly less relevant here and the FPV measure would simply be identical to the GPV measure.

  10. Data on marginality come from Soroka and Wlezien (2010). Note that for the United States we re-estimated our analyses while using presidential vote margins, which mirror the findings based on congressional vote margins.

  11. Data on Kayser and Lindstädt’s (2015) LPR measure are available here: http://mark-kayser.com/data.html.

  12. Given the concern around the use of the lagged dependent variable (LDV) whereby its inclusion would depress the explanatory power of main explanatory factors and absorb part of the trend in the dependent variable (Achen 2000; Plümper et al. 2005), we re-estimated our models without the [POLICY (t − 1)] variable and our substantive conclusions do not change. Hence, we preferred to present in the paper results from the models that control for the past level of spending. However, the analyses without the LDV are reported in Tables S49–S51.

  13. We considered the possibility that 1 year lag might not be enough for policy to respond. Thus we re-estimated our analyses with public preferences and the dynamic measures of electoral vulnerability variables lagged of 2 years. Although these analyses should be taken with extra caution given our already small N, we found no particular evidence of such a delayed (conditional) effect. The analyses are reported in Tables S70–S72.

  14. Given the way the lagged electoral vulnerability variables are created, in the empirical analyses we omit country-years when a new government emerged whose ideology differed from the previous government. This is because in these years the lagged levels of government vulnerability pertain to different governments. However, we consider successive governments with the same Prime Minister (or President) as the same and include country-years where there was continuity in the governing party but a new President (Prime Minister), for the incoming head of government was closely associated with the outgoing leader’s government (see Bernardi and Adams 2017). We re-estimated our analyses (reported in Tables S67–S69) while including those few omitted observations and our substantive conclusions do not change.

  15. We use the partisanship variables available in the same data sets of the spending and preferences data (see footnote 6).

  16. SUR models are preferred to OLS models since our dependent variables are unlikely to be independent, as they are part of the same budget. We thank the anonymous reviewer for this suggestion. Further, we note that, given our small N, in the paper we only report the results for our basic models without over controlling for any additional factors. In particular, since controlling for economic indicators does not subvert the validity of the main conclusions drawn from our basic models (these analyses are reported in Table S64–S66), we opted for a parsimonious strategy and decided to exclude such variables from the analyses. Also, as some readers might want to see the analyses for the Electoral Vulnerability Hypothesis and the Electoral Proximity Hypothesis controlling for the other electoral incentive, we report these analyses in Tables S52–S63.

  17. The analyses with GPU are excluded in the UK because the indicator never falls within the values identified for uncertainty in Table 1. We also note that in UK analyses, the partisan variable is omitted because all governments are from the Conservative Party.

  18. For the US we only report GPV and GPU but not FPV and FPU because both sets of indicators are always computed between Democrats and Republicans, and so the measures are identical.

  19. Though not advisable with very small number of observations (e.g., Jennings 2013), as a final test, we have also re-estimated our analyses by using an error correction model (ECM) in order to capture some short- and long-term effects (analyses are available upon request). Although these analyses should be taken with extra caution, only in a handful of occasions the interaction between changes in public opinion and electoral incentives was statistically significant in the expected direction, supporting our findings of a limited impact of electoral incentives on policy responsiveness.

  20. Note that whether the sign of the coefficient for public preferences in the policy representation analyses should be positive, the sign of the coefficient for policy in the public responsiveness analyses can be either negative, if a negative feedback prevails, or positive, if a positive feedback prevails (for a full discussion on feedback, see Soroka and Wlezien 2010, pp. 29–30). The dependent variable in the public responsiveness model is estimated in levels (e.g., see Soroka and Wlezien 2005). Like in previous analyses, the analyses on public responsiveness control for the lagged dependent variable, which indeed appears to be strongly significant in all instances. Without the inclusion of the lagged dependent variable we find four more cases of public responsiveness (Tables S44, S46 and S48). However, this difference does not undermine the conclusions we can draw from Table 3.

  21. However, we tried whether past spending influences opinion change conditional on (current and past) electoral vulnerability but we did not find much evidence of elite manipulation. Analyses are available upon request.

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Acknowledgements

Several people provided helpful comments on this research and on older versions of this paper. Among others, I wish to thank Jim Adams, Shaun Bevan, Daniel Bischof, Mark Franklin, Sara Hobolt, Will Jennings, Laura Morales, Stuart Soroka, Rick Whitaker, and Chris Wlezien. Different versions of this paper were presented at the ECPR Joint Sessions 2013, ECPR General Conference 2013 and MPSA 2015, and I am grateful for the feedback received. Lastly, I wish to thank the editor and the two anonymous reviewers for helping me improve the final version of this research.

Funding

The research leading to these results has received funding from the European Research Council under the European Commission’s Seventh Framework Programme through a Starting Grant (FP7/2007-2013 Grant Agreement 284277) to the project “Democratic Responsiveness in Comparative Perspective: How Do Democratic Governments Respond to Different Expressions of Public Opinion? (ResponsiveGov)” (http://www.responsivegov.eu/) led by Prof Laura Morales.

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Correspondence to Luca Bernardi.

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Bernardi, L. Policy Responsiveness and Electoral Incentives: A (Re)assessment. Polit Behav 42, 165–188 (2020). https://doi.org/10.1007/s11109-018-9490-4

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  • DOI: https://doi.org/10.1007/s11109-018-9490-4

Keywords

  • Policy responsiveness
  • Electoral pressures
  • Spending
  • Public preferences