UBC Theses and Dissertations

UBC Theses Logo

UBC Theses and Dissertations

Essays in Chinese political economy Wiebe, Michael 2020

Your browser doesn't seem to have a PDF viewer, please download the PDF to view this item.

Notice for Google Chrome users:
If you are having trouble viewing or searching the PDF with Google Chrome, please download it here instead.

Item Metadata

Download

Media
24-ubc_2021_may_wiebe_michael.pdf [ 4.28MB ]
Metadata
JSON: 24-1.0395341.json
JSON-LD: 24-1.0395341-ld.json
RDF/XML (Pretty): 24-1.0395341-rdf.xml
RDF/JSON: 24-1.0395341-rdf.json
Turtle: 24-1.0395341-turtle.txt
N-Triples: 24-1.0395341-rdf-ntriples.txt
Original Record: 24-1.0395341-source.json
Full Text
24-1.0395341-fulltext.txt
Citation
24-1.0395341.ris

Full Text

Essays in Chinese Political EconomybyMichael WiebeB.Sc., University of Manitoba, 2013M.A., University of Western Ontario, 2014A THESIS SUBMITTED IN PARTIAL FULFILLMENT OFTHE REQUIREMENTS FOR THE DEGREE OFDOCTOR OF PHILOSOPHYinThe Faculty of Graduate and Postdoctoral Studies(Economics)THE UNIVERSITY OF BRITISH COLUMBIA(Vancouver)December 2020c© Michael Wiebe 2020The following individuals certify that they have read, and recommend to the Faculty of Graduateand Postdoctoral Studies for acceptance, the dissertation titled:Essays in Chinese Political Economysubmitted by Michael Wiebein partial fulfillment of the requirements for the degree of Doctor of Philosophy in Economics.Examining Committee:Patrick Francois, Professor, Economics, UBCCo-SupervisorThorsten Rogall, Assistant Professor, Economics, UBCCo-SupervisorFlorian Hoffman, Associate Professor, Economics, UBCUniversity ExaminerYves Tiberghien, Professor, Political Science, UBCUniversity ExaminerRuixue Jia, Associate Professor, Economics, UCSDExternal ExaminerAdditional Supervisory Committee Member:Munir Squires, Assistant Professor, Economics, UBCSupervisory Committee MemberiiAbstractChina has sustained incredible double-digit economic growth over three decades. In Chapter 2, Iinvestigate one common explanation for this: meritocratic promotion, where officials at the samelevel compete with each other on the basis of relative GDP growth, and the winners are rewardedwith promotion up the administrative hierarchy. This tournament competition generates strongincentives for politicians to boost growth. However, studying prefecture leaders, I find no evidenceof meritocracy. My null result is stable across different definitions of promotion, regression models,and measures of GDP growth. I rule out possible alternative explanations. Meritocracy is not beingimplemented separately for politically connected and unconnected leaders, or for leaders who areenvironmentally friendly. Moreover, the 2012 corruption crackdown has not effected a structuralchange in promotion criteria.In Chapter 3, I reanalyze the literature on meritocratic promotion. Replicating five papers,I find that the evidence for prefecture leaders is not robust to reasonable specification choices. Iconclude that my null result is not contradicted by the literature. However, I do find some evidenceof meritocracy for county leaders, and propose a model where county-level meritocracy can be anexplanation for China’s economic growth, by incentivizing county leaders and selecting higher-levelleaders based on ability to grow the economy.The co-authored Chapter 4 studies the role of tax collector discretion in preventing tax evasion inChina. The motivating puzzle is that firms bunch above, rather than below, notches in the corporatetax schedule. We propose a model where tax collectors use an enforcement technology, discretionover prepayments, to prevent firms from evading. Tax collectors assign higher prepayment ratesto suspected tax evaders, as a signal to deter evasion. In response, firms do not evade, and bunchabove the notch. To corroborate this interpretation, we study a policy reform that removed taxcollector discretion over prepayments. Following the reform, bunching above the notches decreasedsubstantially. Without their enforcement technology, tax collectors were no longer able to preventevasion.iiiLay summaryChina has sustained incredible double-digit economic growth over three decades. In Chapter 2, Iinvestigate one common explanation for this: meritocratic promotion, where mayors with higherGDP growth are more likely to be promoted; this system incentivizes mayors to boost GDP.However, studying prefecture leaders, I find no evidence of meritocracy. In Chapter 3, I reanalyzethe literature on meritocratic promotion. I find that the evidence for prefecture leaders is notrobust, so my null result is not contradicted by the literature. However, I do find some evidenceof meritocracy for county leaders, and propose a model where county-level meritocracy can be anexplanation for China’s economic growth. Chapter 4 studies a puzzle: faced with a sharp drop intaxes at an income threshold, firms bunch above the threshold, and seemingly choose to pay highertaxes. The explanation is that tax collectors are able to prevent evasion.ivPrefaceChapters 2 and 3 of the thesis are original, unpublished, and independent work. Chapter 4 isco-authored with Jeff Hicks (Vancouver School of Economics, University of British Columbia) andWei Cui (Allard Law School, University of British Columbia). I cleaned the raw data, worked withJeff on data analysis and formulating the model, and collaborated with Jeff and Wei in writing thedraft. The copyright to Chapter 4 is held jointly by the three co-authors.vTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ixList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiii1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Does meritocratic promotionexplain China’s growth? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 52.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 52.2 Institutional context . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 62.3 Literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72.3.1 Provincial leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72.3.2 Prefecture leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72.3.3 County leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82.3.4 Related literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112.5.1 Empirical specification . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112.5.2 Regression results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122.5.3 Power analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122.5.4 Robustness checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132.5.5 Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152.6 Extensions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 15vi2.6.1 Political connections . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152.6.2 Pollution . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 172.6.3 Corruption crackdown . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 172.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182.8 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 193 Reanalyzing the literature on meritocratic promotion . . . . . . . . . . . . . . . 283.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 283.2 Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 293.3 Li et al. (2019) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 323.4 Chen and Kung (2019) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 343.5 Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 363.6 Lorentzen and Lu (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 383.7 Historical meritocracy for provincial leaders? . . . . . . . . . . . . . . . . . . . . . . 393.8 Meritocracy for county leaders? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 403.9 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 413.10 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 434 Bunching on the wrong side:Tax enforcement technologyand tax evasion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 564.1 Institutional details . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 584.1.1 Small business preferential tax rates . . . . . . . . . . . . . . . . . . . . . . . 584.1.2 Prepayments . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 584.1.3 Offsets and refunds . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 594.2 Bunching-above and prepayments . . . . . . . . . . . . . . . . . . . . . . . . . . . . 594.2.1 Substantial bunching occurs below the threshold . . . . . . . . . . . . . . . . 594.2.2 Substantial bunching occurs above the threshold . . . . . . . . . . . . . . . . 604.2.3 Bunching-above is strongly predicted by prepayments . . . . . . . . . . . . . 604.2.4 Additional results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 614.3 Model and evidence . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 614.3.1 Mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 614.3.2 Evidence from a policy reform . . . . . . . . . . . . . . . . . . . . . . . . . . 624.4 Alternative explanations for bunching-above . . . . . . . . . . . . . . . . . . . . . . 644.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 654.6 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 665 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74viiBibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 76AppendicesA Appendix to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 80A.1 A model of a promotion tournament . . . . . . . . . . . . . . . . . . . . . . . . . . . 80A.2 Promotion definitions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 80A.3 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 104B.1 Literature characteristics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 105B.2 Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 107B.3 Li et al. (2019) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119B.4 Chen and Kung (2019) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 121B.5 Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 124B.6 Lorentzen and Lu (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128C Appendix to Chapter 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133C.1 Persistence of bunching . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133C.2 The composition of bunchers . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135C.3 2014 Policy directive . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 137viiiList of Tables2.1 Summary statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 192.2 No effect of GDP growth on promotion . . . . . . . . . . . . . . . . . . . . . . . . . . 202.3 Regions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222.4 Eras . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222.5 Heterogeneous effects by region . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 232.6 Heterogeneous effects by era . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 242.7 Summary stats: political connections . . . . . . . . . . . . . . . . . . . . . . . . . . . 242.8 Controlling for political connections . . . . . . . . . . . . . . . . . . . . . . . . . . . 252.9 Interacting growth × connections . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 252.10 Pollution results: SO2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 262.11 Pollution results: PM2.5 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 262.12 Corruption crackdown . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 273.1 Direct replication of Table 4, Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . 443.2 Reanalysis of Table 4, Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . 453.3 Replication of Table 5 in Li et al.(2019): LPM . . . . . . . . . . . . . . . . . . . . . 473.4 Number of times Promotion = 1 by spell . . . . . . . . . . . . . . . . . . . . . . . . 473.5 Replication of Table IX, Chen and Kung (2019) . . . . . . . . . . . . . . . . . . . . . 483.6 Provincial leaders, Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . 493.7 Prefecture leaders, Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . 503.8 County leaders, Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . 513.9 Nonmeritocratic promotion in Tiger provinces? . . . . . . . . . . . . . . . . . . . . . 523.10 Provincial leaders: Jia et al. (2015) . . . . . . . . . . . . . . . . . . . . . . . . . . . . 533.11 County secretaries: Chen and Kung (2016) . . . . . . . . . . . . . . . . . . . . . . . 543.12 County leaders: Landry et al. (2018) . . . . . . . . . . . . . . . . . . . . . . . . . . . 55A.1 LPM: results for tenure and education . . . . . . . . . . . . . . . . . . . . . . . . . . 83A.2 LPM: clustering at province-year level . . . . . . . . . . . . . . . . . . . . . . . . . . 84A.3 LPM: clustering at province level . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85A.4 Adding covariates in series . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87A.5 GDP growth above the target . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 88ixA.6 Consecutive years above the growth target . . . . . . . . . . . . . . . . . . . . . . . . 89A.7 Consecutive years below the growth target . . . . . . . . . . . . . . . . . . . . . . . . 90A.8 Does meritocration promotion vary by prefecture type? . . . . . . . . . . . . . . . . 91A.9 Dropping mayors promoted in first year . . . . . . . . . . . . . . . . . . . . . . . . . 92A.10 Interaction with autonomous dummy . . . . . . . . . . . . . . . . . . . . . . . . . . . 93A.11 Growth relative to predecessor’s average . . . . . . . . . . . . . . . . . . . . . . . . . 94A.12 Growth relative to provincial average and predecessor’s average . . . . . . . . . . . . 95A.13 Indicator variable for maximum growth . . . . . . . . . . . . . . . . . . . . . . . . . 96A.14 Indicator variable for growth above median . . . . . . . . . . . . . . . . . . . . . . . 97A.15 Indicator variable for growth quartiles . . . . . . . . . . . . . . . . . . . . . . . . . . 98A.16 Calculate provincial average excluding i . . . . . . . . . . . . . . . . . . . . . . . . . 99A.17 Chen and Kung (2019): prefecture secretaries . . . . . . . . . . . . . . . . . . . . . . 100A.18 Yao and Zhang (2015): prefecture secretaries . . . . . . . . . . . . . . . . . . . . . . 101A.19 Li et al. (2019): prefecture secretaries . . . . . . . . . . . . . . . . . . . . . . . . . . 102A.20 Landry et al. (2018): prefecture secretaries . . . . . . . . . . . . . . . . . . . . . . . 103B.1 Article characteristics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 106B.2 Reanalysis of Table 5, Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . 116B.3 Reanalysis of Table 6, Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . 117B.4 Reanalysis of Table 7, Yao and Zhang (2015) . . . . . . . . . . . . . . . . . . . . . . 118B.5 Replication of Table 5 (Li et al., 2019): logit model . . . . . . . . . . . . . . . . . . . 119B.6 Verification of Table IX, Chen and Kung (2019) . . . . . . . . . . . . . . . . . . . . . 121B.7 Replication of Table IX, Chen and Kung (2019): corrected promotion variable . . . . 122B.8 Replication of Table IX, Chen and Kung (2019): promotion definition 1 . . . . . . . 122B.9 Replication of Table IX, Chen and Kung (2019): promotion definition 3 . . . . . . . 123B.10 Replication of Table IX, Chen and Kung (2019): promotion definition 4 . . . . . . . 123B.11 Direct replication: province leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125B.12 Direct replication: prefecture leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . 126B.13 Direct replication: county leaders . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127B.14 Nonmeritocratic promotion in Tiger provinces? Promotion definition 1 . . . . . . . . 129B.15 Nonmeritocratic promotion in Tiger provinces? Promotion definition 3 . . . . . . . . 130B.16 Nonmeritocratic promotion in Tiger provinces? Promotion definition 4 . . . . . . . . 131B.17 Tiger provinces: cumulative average GDP growth . . . . . . . . . . . . . . . . . . . . 132C.1 Predictors of bunching-below vs. -above (pre-reform) . . . . . . . . . . . . . . . . . . 136xList of Figures2.1 Robustness checks: linear probability model . . . . . . . . . . . . . . . . . . . . . . . 213.1 Li et al. (2019), Table 5 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 463.2 Promotion rate: prefecture mayors . . . . . . . . . . . . . . . . . . . . . . . . . . . . 473.3 Promotion rate: prefecture mayors . . . . . . . . . . . . . . . . . . . . . . . . . . . . 484.1 Evolution of the corporate income tax schedule for eligible firms . . . . . . . . . . . 664.2 Bunching at the micro-enterprise thresholds . . . . . . . . . . . . . . . . . . . . . . . 674.3 Bunching at the small-enterprise threshold . . . . . . . . . . . . . . . . . . . . . . . . 684.4 Bunching by prepayment grouping . . . . . . . . . . . . . . . . . . . . . . . . . . . . 694.5 Tax prepayments and bunching-above, micro enterprise thresholds . . . . . . . . . . 704.6 Ratio of bunching-above to bunching-below . . . . . . . . . . . . . . . . . . . . . . . 714.7 Decrease in proportion of bunchers in middle prepayment region . . . . . . . . . . . 724.8 Regression discontinuity estimate of P(bunching-above) at lower prepayment threshold 73A.1 Heterogeneity by year . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 86B.1 Yao and Zhang (2015), Table 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 108B.2 Yao and Zhang (2015), Table 4 (continued) . . . . . . . . . . . . . . . . . . . . . . . 109B.3 Yao and Zhang (2015), Table 5 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110B.4 Yao and Zhang (2015), Table 5 (continued) . . . . . . . . . . . . . . . . . . . . . . . 111B.5 Yao and Zhang (2015), Table 6 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112B.6 Yao and Zhang (2015), Table 6 (continued) . . . . . . . . . . . . . . . . . . . . . . . 113B.7 Yao and Zhang (2015), Table 7 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114B.8 Yao and Zhang (2015), Table 7 (continued) . . . . . . . . . . . . . . . . . . . . . . . 115B.9 Sample size: Li et al. (2019) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 120B.10 Lorentzen and Lu (2018), Table 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128C.1 Persistence of bunching status . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134C.2 Prepayment Descriptives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 139C.3 Composition of bunchers by prepayment region . . . . . . . . . . . . . . . . . . . . . 140C.4 Prepayment behavior over time: Micro-enterprise thresholds . . . . . . . . . . . . . . 141xiC.5 Prepayment behavior over time: Small-enterprise thresholds . . . . . . . . . . . . . . 142C.6 Number of refunds granted . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 143xiiAcknowledgementsI thank my committee members, Patrick Francois, Thorsten Rogall, and Munir Squires for guidingmy thesis. I thank them along with Matilde Bombardini, Matt Lowe, and Jamie McCasland forhelpful feedback on my research.I thank my colleagues for bouncing research ideas and general intellectual enrichment: AnujitChakraborty, Tom Cornwall, Matt Courchene, Alastair Fraser, Nicolas Franz-Pattillo, Brad Hack-inen, Jeff Hicks, Hugo Jales, David Macdonald, Ben Milner, Aruni Mitra, T´ımea Molna´r, AdlaiNewson, Juan Felipe Rian˜o, Victor Saldarriaga, Rogerio Santarrosa, Jacob Schwartz, and MengyingWei.I thank my girlfriend, Laura, for providing a loving respite from the world of research.xiiiChapter 1IntroductionThis thesis studies political economy questions in China. Chapter 2 investigates whether Chinahas used meritocratic promotion of prefecture mayors as a way of incentivizing economic growth,and hence whether meritocracy can explain China’s rapid economic growth. After determiningthat meritocracy is not implemented at the prefecture level, Chapter 3 reanalyzes the literature onmeritocratic promotion, to evaluate the robustness of the evidence. Chapter 4 focuses on corporatetax evasion, studying how tax collectors can use discretion to prevent firms from evading taxes.China’s economy has grown spectacularly over the past three decades, averaging nearly double-digit GDP growth rates, and lifting hundreds of millions of people out of poverty. What canexplain this phenomenon? Recently, a sizeable literature has emerged claiming that China usespromotion tournaments to incentivize economic growth. Officials at the same level (for example,prefecture mayors within the same province) compete with each other on the basis of relativeGDP growth, and the winners are rewarded with promotion up the administrative hierarchy. Thistournament competition generates strong incentives for politicians to boost growth, and henceprovides an explanation for China’s incredible economic performance. Chapter 2 evaluates theempirical evidence for this hypothesis.The seminal work in this literature is Li and Zhou (2005), which found a meritocratic effectfor provincial leaders. This paper has been cited nearly 1000 times, indicating that meritocraticpromotion is a well-accepted idea. For example, in a paper on a different topic, Wang (2016)includes this description: “[T]he promotion of local officials largely depends on their ability toboost economic growth (Li and Zhou, 2005)”. In a review article in the Journal of EconomicLiterature, Brandt et al. (2014) write: “performance evaluation [...] assigned major weight to localGDP growth [...] these policies are widely viewed as having inspired tournament-like competitionamong county and provincial leaders, who [...] made strenuous efforts to ramp up local economies(Li and Zhou 2005)”.Despite this seeming consensus, there is some debate over meritocracy for provincial leaders.Shih et al. (2012) contends that political connections are what determine promotion, rather thaneconomic performance. In contrast, Jia et al. (2015) finds that meritocracy exists, but only forconnected leaders. And Su et al. (2012) claims that the original result in Li and Zhou (2005) doesnot replicate. Lorentzen and Lu (2018) sums up this debate as follows: “Although the evidenceis mixed regarding the promotion of senior officials at or above the provincial level, studies haveconfirmed the existence of meritocracy at lower levels, such as prefectural cities and townships”.1Meanwhile, taking as given the result of meritocratic promotion via tournament competition,economic theorists have been hard at work, building on the theoretical foundations of mechanismdesign to write papers on applied theory that have real world relevance.1But is it wise to take this result as foundational? Given the debate over meritocracy at theprovincial level, we might be skeptical about the findings at the prefecture and county levels,since fewer papers have been published using that data. Moreover, the evidence for meritocracy isnot actually very strong. Yao and Zhang (2015) reports an interaction effect between prefectureleader ability and age, but does not find an average effect of ability on promotion. Landry etal. (2018) finds a positive correlation for county officials, but not for prefecture officals. If theChinese government was actually implementing promotion tournaments in order to incentivizegrowth, we should detect a clear average correlation between growth and promotion, rather thanmere interaction effects.I show that such skepticism is substantiated by the data, at least for prefecture politicians.Focusing on prefecture mayors over 1998-2017, I find no evidence that officials with higher GDPgrowth are more likely to be promoted. Given the variety of ‘promotion’ definitions in the literature,I collected finely coded career histories, which allow me to show that my results are robust to fourdifferent definitions of promotion. My results are stable across many different regression specifica-tions. In every case, whether varying control variables, measures of GDP growth, or using logisticand ordered logistic regression instead of a linear probability model, I find no correlation betweengrowth and promotion. I also rule out possible alternative explanations for my null result. I findno heterogeneous effects over time or by region. I show that meritocracy is not being implementedseparately for politically connected and unconnected leaders, or for leaders who are environmentallyfriendly. I also show that the 2012 corruption crackdown has not effected a structural change inthe promotion of prefecture leaders.In Chapter 2, I found no evidence for meritocratic promotion of prefecture leaders. And yet,there are many papers in the literature that claim to provide evidence for meritocracy at theprefecture level. How can this tension be resolved? In Chapter 3, I revisit five papers from thisliterature.Digging into these papers, I find that their prefecture results are not robust to reasonablespecification choices, and in one case, are due to possible data errors. In each case, I find that thepaper does not provide robust evidence for meritocratic promotion. I conclude that my results inChapter 2 are sound, and that the papers in this literature contain flaws.To preview my results, I replicate papers published in the Journal of Economic Growth (Yao andZhang, 2015), the Economic Journal (Li et al., 2019), the Quarterly Journal of Economics (Chenand Kung, 2019), Comparative Political Studies (Landry et al., 2018), as well as a working paper(Lorentzen and Lu, 2018). I find that the results for meritocratic promotion of prefecture leaders1Just in the past two years, there have been four theory papers written on meritocratic promotion: Chen et al.(2019), Li et al. (2019), Xiong (2019), and Wang and Zheng (2020).2in four papers (Yao and Zhang, 2015; Li et al., 2019; Landry et al., 2018; Lorentzen and Lu, 2018)are replicable using their own data and code, but are not robust to different specifications. I findthat the results in the final paper (Chen and Kung, 2019) are possibly due to data errors. UsingClemens (2017)’s terminology, I am performing a reanalysis in the former cases, and a verificationin the latter case.2Lastly, I re-examine the evidence for meritocracy at the province and county levels. At theprovince level, a new paper (Sheng, 2020) claims to find evidence for meritocratic promotion onlyfor provincial governors during the Jiang Zemin era (1990-2002). I test this hypothesis using thedata from Jia et al. (2015) and find no such effect. For county leaders, the two papers on county-level politicians (Chen and Kung, 2016; Landry et al., 2018) use non-standard specifications, so Ire-analyze their data using my preferred specification: regressing an annual promotion variable oncumulative average relative GDP growth. In this case I find suggestive evidence for meritocracybeing implemented for county leaders. I conclude by proposing a model of meritocracy wherecounty-level promotion tournaments provide a causal explanation for China’s economic growth, byincentivizing county leaders and selecting higher-level leaders based on ability to grow the economy.Turning from politicians to firms, Chapter 4 studies strategic interactions between firms andtax collectors. China’s corporate income tax provides preferential rates to small firms through aseries of notches in the tax schedule.3 Firms with reported taxable income below a given thresholdreceive average tax rates that are 5 to 15 percentage points lower relative to firms immediatelyabove the threshold. This strongly incentivizes firms to report income below the threshold. Ourmotivating puzzle is that a significant mass of firms bunch above the notches rather than below.Using data from tax returns, we show that bunching-above is explained by tax collectors using anenforcement technology, discretion over regulatory procedures, to prevent tax evasion.Tax collectors exercise discretion over a firm’s tax prepayments, which are made quarterlythroughout the year. Specifically, tax collectors decide whether firms prepay at the preferentialrate or the (higher) standard rate. If tax collectors can imperfectly observe whether firms areeligible for the lower rate, they might assign higher prepayment rates to suspected-ineligible firms.This signals to the firm a willingness to audit if the firm reports year-end income below the threshold(and thereby claims the lower tax rate). In response, wanting to avoid a costly audit, these firmsreport income above the threshold, generating the observed bunching-above behavior.To validate this model, we start by showing a strong correlation between prepayments andbunching-above. Firms that prepay at a rate higher than the preferential rate are much more likely2Clemens distinguishes between replication and robustness. Replication includes verification (same specification,same population, and the same sample) and reproduction (same specification, same population, and a differentsample). Robustness includes reanalysis (different specification, same population, and possibly the same sample)and extension (same specification, different population, and a different sample). In my case, I am using the samedata as the original paper, but changing the specification. For Chen and Kung (2019), data errors count as a failedverification.3A notch is a discrete change in the average tax rate; a kink is a discrete change in the marginal tax rate. Notchesare a common feature of many tax systems (Kleven, 2016).3to bunch above the income threshold, consistent with our story of ineligible firms being assignedhigher prepayment rates. We then study a policy reform that removed tax collector discretionover prepayments. Following the reform, we observe a sharp drop in firms prepaying more thanthe preferential rate, as well as an increase in bunching-below and a decrease in bunching-above.These findings suggest that, without their enforcement technology, tax collectors were no longerable to prevent ineligible firms from evading taxes by claiming the lower rate. Facing no barriersto evasion, firms claimed the lower rate, generating the expected bunching below the threshold.Thus, we observe the outcomes of a tax enforcement game, where firms try to evade taxes,and tax collectors try to stop them. Unique to our context, tax collectors started out possessingan enforcement technology to prevent evasion, which leads to firms bunching above the threshold.When tax collectors lost this enforcement technology, firms bunch below, as is common in othersettings.4Chapter 2Does meritocratic promotionexplain China’s growth?2.1 IntroductionChina’s economy has grown spectacularly over the past three decades, averaging nearly double-digit GDP growth rates, and lifting hundreds of millions of people out of poverty. What can explainthis phenomenon? Recently, a sizeable literature has emerged claiming that China uses promotiontournaments to incentivize economic growth. Officials at the same level (for example, prefecturemayors within the same province) compete with each other on the basis of relative GDP growth,and the winners are rewarded with promotion up the administrative hierarchy. This tournamentcompetition generates strong incentives for politicians to boost growth, and hence provides anexplanation for China’s incredible economic performance. This chapter evaluates the empiricalevidence for this hypothesis at the prefecture level.Focusing on prefecture mayors over 1998-2017, I find no evidence that officials with higherGDP growth are more likely to be promoted. Given the variety of ‘promotion’ definitions inthe literature, I collected finely coded career histories, which allow me to show that my resultsare robust to four different definitions of promotion. My results are stable across many differentregression specifications. In every case, whether varying control variables, measures of GDP growth,or using logistic and ordered logistic regression instead of a linear probability model, I find nocorrelation between growth and promotion. I also rule out possible alternative explanations for mynull result. I find no heterogeneous effects over time or by region. I show that meritocracy is notbeing implemented separately for politically connected and unconnected leaders, or for leaders whoare environmentally friendly. I also show that the 2012 corruption crackdown has not effected astructural change in the promotion of prefecture leaders.The remainder of the chapter is structured as follows: Section 2.2 discusses the institutionalcontext, while Section 2.3 summarizes the literature on meritocratic promotion at the province,prefecture, and county levels. Section 2.4 presents my data on prefecture mayors. Moving to thenull result, I show in Section 2.5 that there is no correlation between promotion and growth. Section2.6 rules out possible alternative explanations. Section 2.7 concludes.52.2 Institutional contextChina’s political system is described as a regionally decentralized authoritarian regime (Xu,2011). While local governments have control over their local economies, the central governmentretains control over personnel appointments via the Organization Department. This control overpersonnel allows the central government to exercise authority over all lower-level governments.4For example, since the central government controls the appointment of provincial leaders to thePolitburo, it can set the policy agenda for the provinces. Similarly, provincial governments controlpersonnel appointments of prefecture leaders, and hence can set policy for prefectures. This logicapplies down to counties and townships.5The upshot of centralized personnel appointments is that the central government can prioritizepolicies like economic growth, and has the means to strongly incentivize the implementation ofthose policies. In this context, scholars have argued that China has implemented a “promotiontournament”, where officials at the same level compete to boost economic growth, and the topperformers are rewarded with promotion to the next level of the bureaucracy (Li and Zhou, 2005;Xu, 2011).6This system of meritocratic political selection, also known as “jurisdictional yardstick competi-tion”, serves as an incentive scheme for politicians to boost economic growth. Thus, provincial lead-ers compete with each other for promotion to the Politburo, prefecture leaders (within a province)compete for promotion to the provincial government, and county leaders (within a prefecture) com-pete for promotion to the prefecture government. As discussed in Section 2.3, scholars have studiedmeritocratic promotion at each of these three levels.74The Chinese administrative hierarchy has five nested levels: center, province, prefecture, county, township.5This is known as the “one-level down” system of cadre management, where officials at a given level are appointedby politicians governing the level immediately above, rather than the central government directly appointing allofficials.6This simple model of the promotion tournament is incomplete. As Wang and Zheng (2020) points out, a rank-order tournament requires a convex pay scale in order to induce an efficient level of effort. That is, the pay increasebetween levels of the bureaucracy must grow as one ascends the hierarchy. This theoretical requirement is contradictedby the empirical reality that the public sector pay scale is concave. Wang and Zheng (2020) solve this puzzle byhypothesizing that Chinese politicians derive income from corruption. Politicians accumulate wealth from corruptionover their careers, and higher-ranked politicians are better able to protect this wealth, by colluding with anti-corruption inspectors. Hence, the de facto pay scale is convex, on this view, and politicians compete for the prize ofkeeping their ill-gotten gains. Thus, a consistent model of the promotion tournament must also presuppose widespreadcorruption, which may be a realistic assumption for post-reform China.7It is not clear how different levels of the tournament interact. For example, as prefectures are nested withinprovinces, it is possible that provincial leaders boost growth indirectly by supervising prefecture officials, who directlymanage the economy. (Of course, this logic can be applied one more level, with prefecture leaders supervising countyofficials, who directly manage the economy.) It seems plausible that higher-level leaders perform a mix of roles,directly managing some parts of the economy, while supervising lower-level officials.62.3 Literature2.3.1 Provincial leadersThe literature on meritocratic promotion started with a pair of papers (Li and Zhou, 2005;Chen, Li, and Zhou, 2005) finding a positive correlation between GDP growth and promotion forprovincial party secretaries and governors. This finding was interpreted as evidence that Chinauses promotion tournaments to incentivize economic growth. These two papers were challengedby Su et al. (2012), which claimed that their results did not replicate after fixing data errors inthe promotion variable. Shih et al. (2012) further disputes the meritocracy narrative, findingthat political connections (based on shared hometown, college, and workplace) explain promotion,rather than economic growth.8Jia et al. (2015), attempts to reconcile these disparate findings, testing for an interactioneffect between political connections and growth.9 The authors find no average effect of growth onpromotion, but do report a positive interaction effect with connections. They interpret this findingas incumbent politicians solving the competence-loyalty tradeoff by selecting competent officialsout of the set of connected (loyal) officials. Note that this framing supports a model of limitedmeritocracy, where connected leaders are evaluated meritocratically, but unconnected leaders arenot. This model does not generate generic incentives for economic growth, and hence does notprovide a general explanation of China’s rapid growth.102.3.2 Prefecture leadersThe literature on prefecture-level meritocratic promotion began with Yao and Zhang (2015).This paper applies the Abowd-Kramarz-Margolis method (for estimating worker and firm fixedeffects) to leaders and prefectures, to estimate both leader ability (to boost growth) and the effectof leader ability on promotion. That is, the authors test for meritocracy by regressing promotionon ability. Despite finding no average effect of ability on promotion, the authors report a positiveinteraction effect between ability and age, and use this finding to frame their results as supportingthe meritocracy hypothesis.118Francois et al. (2020) finds that similar-ranking politicians working in the same department are actually morelikely to belong to different factions. This result casts doubt on using shared workplace as a measure of politicalconnections.9The authors find an interaction effect for connections based on shared workplace, but not for shared hometownor college.10Fisman et al. (2020) further studies the role of political connections, finding that hometown and college con-nections are actually negatively correlated with promotion, after controlling for city and college fixed effects. This“connections penalty” is stronger during the anti-factionalist Mao era, suggesting that promotions of connectedofficials were viewed as factionalism.11I discuss in Chaper 2 how this age-ability interaction can be interpreted as supporting a limited version ofmeritocratic promotion. Briefly, the problem is that meritocratic promotion only for old leaders does not incentivizeyoung leaders to boost growth, contradicting the notion of meritocratic promotion as a general incentive scheme.7Landry et al. (2018) studied meritocracy using a linear probability model for prefecture leadersover 1999-2007. The authors report finding no correlation, but in contrast to the literature, theyuse spell-level data rather than a prefecture-year panel. Hence, their independent variable is aleader’s average growth over their tenure, rather than cumulative average growth in each year.In an appendix result, Jiang (2018) uses a survival model, following prefecture mayors andsecretaries until they are promoted or retire. In contrast, every other paper in this literature usesjurisdiction-year panel data, measuring promotion using a politician’s next position in the yearafter they leave office. Jiang (2018) finds an effect of growth on promotion for politically connectedleaders, but not for unconnected leaders.12 The paper does not test for a generic meritocracyeffect for prefecture leaders (that is, whether there is an average growth-promotion correlation,abstracting away from political connections).In a paper on land corruption, Chen and Kung (2019) includes secondary results on meritocraticpromotion. Their main result is that local politicians give deals on land sales to Politburo-connectedfirms, and these politicians are in turn more likely to be promoted; these correlations are interpretedas corruption. They find that land sales predict promotion for secretaries, but not mayors; whileGDP growth predicts promotion for mayors, but not secretaries. (They find an identical pattern atthe provincial level for secretaries and governors.) They conclude that mayors (but not secretaries)compete in a promotion tournament based on growth.13Finally, Li et al. (2019) studies GDP targets, explaining why targets increase in magnitude atlower levels of government. They write a formal model that assumes meritocratic promotion, andreport a novel result: the effect of growth on promotion is increasing in the growth target. Theirpaper uses maximum likelihood estimation where the link function is a contest success function.Validating their assumption, they find a positive correlation between growth and promotion.Overall, there is a surprising amount of variety in the empirical methods used in the literatureon prefecture leaders. Despite this, almost every paper finds evidence for meritocratic promotion,confirming the narrative first established by Li and Zhou (2005).2.3.3 County leadersThere are two papers studying meritocratic promotion at the county level (Chen and Kung,2015; Landry et al., 2018).14 Chen and Kung (2015) studies the interaction between land corruptionand meritocratic promotion for county secretaries over 2000-2008. They find a positive correlationbetween promotion and the annual per capita GDP growth rate (they do not report results forgrowth relative to the prefecture average or for cumulative average growth over a secretary’s term).Landry et al. (2018) study meritocratic promotion for county mayors and secretaries over12However, the paper does show that these effects are statistically different.13As I discuss in Chapter 3, their promotion data for prefecture mayors is possibly flawed due to data errors.14County-level studies are less common because of the daunting task of collecting GDP and promotion data for thenearly 3000 county-level divisions in China.81999-2007. Using term-level data on relative GDP growth, they find a positive correlation betweengrowth and promotion for both mayors and secretaries. Finding consistent results across two studiessuggests that the meritocracy hypothesis is strongly supported at the county level. This may betrue, but given the course of the provincial and prefecture literatures (strong initial results thatare contradicted by follow-up papers), it seems wise to wait for further county-level studies beforemaking strong updates.2.3.4 Related literatureSerrato et al. (2019) finds seemingly meritocratic promotion based on enforcement of the One-Child Policy. But in fact promotion was not meritocratic, as leaders were able to manipulate thepopulation data. Thus, promotion appears meritocratic when using self-reported (manipulated)data, but is not when using unmanipulated census data. In my context, it is possible that mayorsmanipulate GDP data by exerting control over the prefecture statistics bureau. However, giventhat I find no correlation between growth and promotion, manipulated GDP data is not a concern.In a study of GDP growth targets, Zhang et al. (2018) finds that actual growth rates arebunched above growth targets. This suggests that politicians take growth targets seriously. Asa robustness check, I will test whether meeting or missing the growth target is correlated withpromotion.2.4 DataI study meritocratic promotion for Chinese prefecture mayors over 1998-2017.15 I am ableto collect data on roughly 300 of China’s 333 prefecture-level jurisdictions. While mayors arethe second-ranked leader below the top-ranked party secretary16, I focus on mayors because itis commonly thought that government executives are in charge of economic activities, while partysecretaries are responsible for social stability.17 Hence, we should observe mayors rather than partysecretaries competing in the promotion tournament.18 (I examine data on prefecture secretaries inSection 2.5.)15Data on mayors and GDP, though available online, is less complete before 1998. Future work could draw on thedata in Serrato et al. (2019) to extend the sample back to 1985.16At each level of government, the top politicians are the party secretary (of the Chinese Communist Party) andthe government executive (i.e., the provincial governor and prefecture/county mayors). The party secretary is thetop-ranked official at each level, while the government executive is ranked below the secretary.17Jia (2017) remarks that provincial party secretaries’ “major responsibilities include the implementation of thecentral government policies and social stability whereas governors key duty is to promote growth.” (fn. 15, p. 12-13)Chen and Kung (2019), in their study of land corruption, conclude that “the governor has to rely on himself forpromotion, specifically by improving economic performance or GDP growth in his jurisdiction [...] only the provincialparty secretaries are being rewarded for their wheeling and dealing.” (p.212) Moreover, Sheng (2020) finds thatmeritocratic promotion was implemented only for provincial governors during the Jiang Zemin era (1990-2002), andnever for provincial party secretaries.18In the prefecture literature, Yao and Zhang (2015) and Li et al. (2019) pool mayors and secretaries. Landry etal. (2018) and Chen and Kung (2019) run separate regressions for mayors and secretaries. As noted in the literature9I collected economic data on prefectures (GDP, population, and revenue) from provincial statis-tical yearbooks. Since the yearbooks are online and require manual data entry from PDFs, I hiredmultiple research assistants to independently collect the same data, in order to rule out data entryerrors. I also collected data on the same variables from CEIC’s China Premium Database.I use the provincial implicit GDP deflator to construct real prefecture GDP from data onnominal GDP. Using provincial data from CEIC, I calculate the annual deflator as the differencebetween the nominal and real GDP growth rates. Real prefecture level GDP is then calculatedas nominal GDP divided by cumulative deflator growth since 1990.19 Given the real GDP level, Icalculate real GDP growth rates. Henceforth, all references to GDP are to real GDP.To test for meritocratic promotion, I estimate the correlation between a mayor’s cumulativeaverage relative GDP growth and a promotion variable. First, for each prefecture I calculate GDPgrowth relative to the annual provincial average. Then I calculate the cumulative average of thisrelative growth for each year of the mayor’s tenure.20 This reflects that provincial elites evaluatemayors on their total performance, and not merely their performance in any single year. (I alsouse annual growth in robustness checks.)I hired RAs to collect data on mayors’ career paths from online CVs, available on Baidu. Eachprefecture-year observation is matched with a mayor, based on being in office for the majority ofthe year. Specifically, if a mayor takes office after July 1 of year t, they are coded as starting theirterm in year t + 1. I used a finely-coded turnover variable to capture subtleties in the adminis-trative hierarchy, with four main categories: retirement/arrest, demotion, horizontal transfer, andpromotion.To avoid data entry errors, I had multiple research assistants collect the same data. Surpris-ingly, these independent data collections initially disagreed on 10-20% of promotion cases. Thesedisagreements stemmed partly from nuances in the variable coding, but also ambiguities in the CVsthemselves.21 I instructed the two RAs to work together with me to discuss the issues22, and col-lectively we resolved all disagreements. My data collection experience underscores the importancesection, Landry et al. (2018) finds no correlation for either prefecture mayors or secretaries, while Chen and Kung(2019) finds a correlation for mayors but not secretaries.19Specifically, for province p and prefecture j, I calculate the annual provincial deflator as deflatorpt =growthnominalpt − growthrealpt , with which I compute cumulative deflator growth since 1990, deflatorGrowthpt. ThenGDP realjt = GDPnominaljt /deflatorGrowthpt.20Note that a regression with the cumulative average of absolute GDP growth and province-year fixed effects willachieve the same outcome (since the fixed effects subtract the annual provincial average), assuming that mayors’spells perfectly overlap. This assumption is not satisfied, since in practice, terms have varying lengths and mayorstake office in different years. Hence, using absolute growth with province-year fixed effects subtracts the annualprovincial mean of the cumulative averages, where the latter are calculated across different years. This approachseems less intuitive.21For example, a mayor can move to an equal-ranking position in the provincial government, which would beclassified as a transfer. However, their CV includes a parenthetical statement indicating that their de facto rank washigher, which should be a promotion.22This worked better than having a third RA perform another independent data collection, since the problem wascoding ambiguities that required careful interpretation, rather than simple data entry errors.10of systematic data collection and definition of the promotion variable. Papers in this literature col-lect their own data and use their own definitions, which could explain any disagreements betweenpapers.Given the possible ambiguities in measuring promotion, I construct four definitions of promotionwith varying strictness to use in robustness checks (see Appendix Section A.2). For example, thestrictest definition counts only moves to higher-ranking provincial positions, while the less restrictivedefinitions include a move from mayor to prefecture party secretary. Papers in the literature havevarying approaches to coding moves to the prefecture or provincial Local People’s Congress (LPC)and Chinese People’s Political Consultative Conference (CPPCC). With my four definitions, I canuse either approach, where these moves are counted as either transfers or promotions. In mypreferred definition, a mayor is promoted if they take a position as a prefecture secretary, a mayorin a sub-provincial city, a higher-ranking position in the provincial or central government, or ahigher-ranking position in the Communist Youth League.I use an annual dummy promotion variable (=1 in the year of promotion, and 0 otherwise) inmy main specification with a linear probability model. I also define an annual ordered categoricalvariable (=0 if retirement/arrest, =1 if demotion, =2 if transfer or stay in office, =3 if promotion)which I use with ordered logistic regressions. I vary the promotion definitions in robustness checks.2.5 Results2.5.1 Empirical specificationTo test for meritocratic promotion, I regress a promotion variable on a mayor’s average GDPgrowth, controlling for prefecture characteristics X, mayor characteristics Z, and fixed effects.Following the literature, my baseline model is a linear probability model as in the following speci-fication:yijpt = β ·Growthijpt + δXjpt + θZijpt + γpt + ijpt (2.1)Here yijpt is the promotion outcome of mayor i in prefecture j in province p in year t. Growthijptis the cumulative average relative GDP growth of mayor i; that is, taking i’s growth relative tothe annual provincial average, it is the average from i’s first year in office until year t. To controlfor selection of connected mayors into fast-growing prefectures, I control for initial (log) GDP andpopulation in Xjpt, as measured in the first year a mayor takes office. Z includes sex, a quadraticin age, a categorical variable for education (with categories for high school, college, masters, andPhD), and dummy variables for tenure (the number of years a leader has served as mayor). AsPersson and Zhuravskaya (2016), studying provincial secretaries, finds that local leaders are lesslikely to be promoted than outsiders, I also control for whether a mayor is governing in theirhometown prefecture. Since each province runs their own annual promotion tournament, I include11a province-year fixed effect γpt. Standard errors are clustered at the prefecture level.If promotion is meritocratic and there is no selection bias, we should observe β > 0. However,without quasi-experimental variation, selection bias is difficult to rule out. It is possible that, say,politically connected leaders are sent to fast-growing prefectures, and are later promoted on thebasis of their connections. Conversely, it is also possible that high ability leaders are sent to slow-growing prefectures to bring up their growth rate. In this case, we should observe β < 0. Hence,my null result could reflect a true absence of meritocracy, or a true meritocratic effect confoundedby some combination of positive and negative selection.2.5.2 Regression resultsTable 2.2 presents my LPM results in Columns 1-3. GDP growth has a negative and non-significant effect on promotion, and the coefficient remains fairly stable when mayor and prefecturecharacteristics are added to the regression. In contrast to the literature, I find no correlationbetween growth and promotion.Age has an inverted-U relationship with promotion, indicating that older mayors are morelikely to be promoted, but also capturing the fact that mayors above the retirement age (60) havelower promotion chances. Tenure and education are both positively correlated with promotion(coefficients for these dummy variables are omitted)23, indicating that there is some meritocraticelement to promotion. Interestingly, mayors serving in their hometown prefecture are much lesslikely to be promoted, even controlling for prefecture type. This could be a selection effect, wherehigh quality leaders (who are likely to reach high office) are appointed as mayors outside of theirhometown. This shuffling could be designed for merely helping ‘groomed’ mayors to gain experience,or to prevent them from forming factional ties in their hometowns.Columns 4-6 and 7-9 repeat the same analysis using logistic and ordered logistic regression,respectively. They both confirm my LPM results, again finding a negative and nonsignificantcoefficient on GDP growth. I conclude that the weaknesses of linear probability models (i.e.,generating predicted values outside of [0, 1]) are not important here.242.5.3 Power analysisGiven that I find a null result, a natural question is whether my analysis is sufficiently poweredto detect a reasonable effect size. In their analysis of provincial leaders, Jia et al. (2015) reportthat a one standard deviation (2.4pp) increase in growth increases the probability of promotionby 1.7pp. I use this effect size (corresponding to a coefficient β = 0.7) to perform a simple powercalculation. First, I assume that the sampling distribution of the estimate is t-distributed with23In Appendix Table A.1, I report the coefficients for tenure and education.24I vary the level of clustering in the LPM in Appendix Tables A.2 and A.3. I find that the main results are stillnonsignificant.12center β, scale s, and degrees of freedom n− k. Since my prefecture GDP data has higher variancethan the provincial data in Jia et al. (2015), I rescale to obtain β = 0.017/0.048 = 0.36. Takingthe standard error s = 0.11 from my LPM results, I calculate that I have 89% power for this effectsize. I conclude that statistical power is not a hindrance to detecting meritocratic promotion.2.5.4 Robustness checksNext, given the variety of regression specifications used in the meritocracy literature, perhaps mynull result is due to not running the correct regression. To check this, I run a battery of robustnesschecks and plot the results in Fig. 2.1. The graph plots the LPM coefficient on GDP growth acrossmany regression specifications. These specifications can vary on: including covariates or not; using(cumulative) average GDP growth versus the annual growth rate; using province-year fixed effects(default) versus separately including province and year fixed effects; including prefecture fixedeffects or not; using per capita GDP versus level GDP to construct the growth rate; and on thestrictness of the promotion definition, which is decreasing in the definition number.The main specification is denoted by the blue marker; this specification includes covariates, uses(cumulative) average GDP growth as the independent variable, uses province-year fixed effects,omits prefecture fixed effects, uses level GDP instead of per capita GDP to construct the growthrate, and uses my second definition of promotion (which includes a mayor moving to prefecturesecretary or higher-ranked provincial positions).As we can see, the coefficient is almost always negative and nonsignificant, and is never positiveand significant. The coefficient is most negative using Definition 4, which is the most expansivedefinition of promotion. Compared to the other definitions, here the most leaders are counted aspromoted, including those with lower growth rates, which generates a more negative correlation.Overall, the coefficients are stable, with the confidence intervals always overlapping.In the Appendix, I perform multiple other robustness checks. Table A.4 shows the main re-gression results when adding covariates one at a time; the coefficients are stably negative andnonsignificant. Next I explore whether promotion decisions are made by comparing prefectureleaders’ GDP growth to the annual growth target set by their provincial government.25 Table A.5tests whether mayors are promoted for having their cumulative average GDP growth higher thanthe provincial target. I find no correlation using either a dummy variable 1{Growth > Target}, adummy for growth exceeding the target by 3pp (representing the 75th percentile of growth relativeto the target), or a continuous variable for distance to the target.Taking another angle, Table A.6 tests whether mayors are promoted for being above the targetin consecutive years. I find a strong positive correlation that disappears once I control for tenure, asbeing above the target in consecutive years is strongly correlated with how many years a mayor has25Data on provincial growth targets is taken from the ”Report on the Work of the Government”, available online.Li et al. (2019) studies GDP growth targets in China.13been in office. To confirm this interpretation, I show in Table A.7 that I get the same pattern whenusing consecutive years below the growth target. Overall, I do not find any evidence that mayorsare evaluated based on their economic performance relative to the target set by their provincialgovernment.A different explanation for my null result is that a positive correlation is being masked byheterogeneity by prefecture type. Prefecture-level jurisdictions can one of three types: prefecture-level cities, prefectures, or autonomous prefectures.26 So far I have been including a separateintercept for each type, but it is possible that different promotion criteria are applied in differenttypes. For example, autonomous prefectures, being located in western provinces, might focus moreon social stability than economic growth, relative to prefecture-level cities. To test this hypothesis,I interact the GDP growth variable with a dummy for prefecture type. The results are presentedin Table A.8. While promotion is much less likely in autonomous prefectures, I find no evidencethat the growth-promotion correlation differs by prefecture type.One worry about the promotion data is that some mayors are promoted during their first yearin office, when it is not clear that GDP data is available to evaluate their growth performance. Inparticular, since GDP data is not released until the following year, the Organization Departmentis seemingly not able to measure GDP growth for mayors promoted during their first year. TableA.9 excludes mayors who are promoted after serving in office for only one year. When excludingthem, however, the coefficient remains negative and nonsignificant.Several papers in the literature calculate GDP growth relative to a leader’s predecessor’s averagegrowth, to capture whether the government evaluates performance by comparing a leader to theirpredecessor. Chen, Li, and Zhou (2005) take this approach for provincial leaders, while Shih et al.(2012) calculates growth relative to both the provincial average as well as the predecessor’s averagegrowth. I implement these methods in Tables A.11 and A.12, and again find no correlation.To further explore the relationship between GDP growth and promotion, I replace my continuousaverage relative growth variable with dummy variables for the maximum growth in a province-year, having growth above the province-year median, and quartiles of GDP growth calculated byprovince-year. The results are reported in Tables A.13, A.14, and A.15, where I find no relationship.Finally, I calculate relative GDP growth by subtracting the provincial average, where the latter iscomputed excluding observation i; I then use this variable to construct cumulative average relativegrowth.27 This is to capture whether the government evaluates the relative performance of mayori by comparing to the performance only of the −i mayors. Table A.16 shows that this change doesnot affect the null result.In Section 2.4, I mentioned that we should observe meritocratic promotion for mayors ratherthan party secretaries. This is because mayors, as the government executive, are in charge of26As of this writing, there are 333 prefecture-level divisions in China, with 293 prefecture-level cities, 7 prefectures,and 33 autonomous prefectures (including leagues).27My baseline results use the provincial average without excluding observation i.14running the economy, while the party secretary is responsible for social stability. To confirm thisassumption, I test for a growth-promotion correlation for prefecture secretaries, using data frompapers in the literature (Chen and Kung, 2019; Yao and Zhang, 2015; Li et al., 2019; and Landryet al. 2018). The results are presented in Tables A.17-A.20. I find no effect of GDP growth onpromotion, measured as annual or cumulative average growth, in either linear probability or logisticregression models. Hence, the meritocratic promotion hypothesis is not supported by the data foreither prefecture mayors or secretaries.I conclude that my null result is robust to different regression models, different samples, anddifferent variable definitions, and reflects the true correlation between GDP growth and promotion.2.5.5 HeterogeneityTo further explore my null result, I examine heterogeneity across space and time. In particular,it is possible that the government uses meritocratic promotion in the rich, fast-growing coastalprovinces, but applies different promotion criteria in the western provinces with large ethnic mi-nority populations (where social stability is more important). I interact GDP growth with regiondummies (see Table 2.3) to test for regional heterogeneity. Furthermore, Sheng (2020) finds thatmeritocracy at the provincial level only existed during the Jiang Zemin era (1993-2002), wheneconomic growth was highly valued by the central government. To test for changes in promotioncriteria over time, I interact GDP growth with dummies for eras corresponding to the generalsecretary (see Table 2.4).Results are presented in Tables 2.5 and 2.6. Column 3 in both tables presents my preferredspecification with full controls. I find no statistically significant differences across regions or eras.28I conclude that my null result is not driven by different regions or eras applying different promotioncriteria, which cancel out and produce a null average effect. Instead, the absence of meritocraticpromotion for prefecture mayors is consistent across regions and eras.292.6 Extensions2.6.1 Political connectionsThe main alternative to the meritocracy hypothesis is that political connections determinepromotion. Rather than the best-performing leaders being promoted, the connections view contendsthat it is the best-connected leaders who advance through the bureaucracy. My null result could28Figure A.1 plots the coefficients from a regression interacting GDP growth with year dummies. I again find nopattern across years. Table A.10 tests whether growth affects promotion differently in autonomous regions (Tibet,Xinjiang, Inner Mongolia, Ningxia, and Guangxi); I find no statistically significant difference.29In unreported results, I calculate the regression weights from Aronow and Samii (2016), which determine theeffective sample used by OLS. I find no striking patterns; the weights are fairly even across regions and eras, confirmingthe interaction results.15be obscuring a real positive correlation, if I do not properly control for connections. While mybaseline results control for a mayor having any poltical connection (either shared hometown, school,or ’patron’, defined below), there is possibly a more subtle relationship between connections andpromotion, where only connected leaders are promoted meritocratically.Studying provincial leaders, Shih et al. (2012) finds that factional ties explain promotion,where ties are defined based on shared birthplace or overlapping time in college or past workplaces.In contrast, Jia et al. (2015) finds a positive interaction effect between workplace connectionsand growth (and no effect for hometown or college ties), concluding that some limited form ofmeritocracy exists, while also providing an answer to the competence-loyalty tradeoff. However,Fisman et al. (2020), studying candidates for the Politburo, finds that hometown and college tieshave a negative effect on promotion (and no effect for workplace ties), after including fixed effectsto control for quality differences. Overall, the literature on provincial leaders is quite mixed.Papers studying prefecture leaders use varying definitions of political connections. Chen andKung (2019) controls for ‘factional ties’, but includes no details on the variable construction beyondciting Shih et al. (2012) and Jia et al. (2015). Li et al. (2019) does not control for connections,while Yao and Zhang (2015) uses provincial experience as a proxy for connections. Jiang (2018)defines connections based on a leader being in office at the same time as the provincial secretarywho appointed them. Landry et al. (2018) uses a similar definition, but also requires that theleader was appointed at least one year after the provincial secretary took office (i.e., leaders are notconnected if they were appointed in the same year that the provincial secretary took office)30.While workplace ties are commonly used, this definition is vulnerable to false positives andselection bias. In particular, if a high ability leader rises to a high-ranking office on the basis oftheir performance, but doesn’t form any connections during that time, they will nevertheless becoded as connected. Moreover, if high-ability leaders are more likely to be promoted, this willgenerate a spurious correlation between connections and promotion.I collected data on shared hometown and college with the provincial secretary and governor.Table 2.7 shows the summary statistics. Roughly 30% of mayors share a home province witha provincial leader (either secretary or governor), while only 4% share a home prefecture (and1% attended the same school). Using Jiang (2018)’s definition, where a mayor’s patron is theprovincial secretary who appointed them, 73% of mayors are in office while their patron is thecurrent provincial secretary.Next I examine whether connections play a role in determining the effect of growth on promotion.Table 2.8 shows that controlling for connections individually has no effect on the growth coefficient.Further, of the connection variables, only the patron variable has a significant effect, but it is30From correspondence with Xiaobo Lu. Note that this does not match the definition used in the text: “a politicalconnection is coded 1 when a prefectural politician experienced a position change under the watch of the provincialparty secretary who appointed them to the current position in the first place, and 0 otherwise.” (Landry et al. 2018,p.1084)16surprisingly negative. This is despite including tenure fixed effects, as by construction, mayors aremore likely to be connected to their patron earlier in their term.To explore whether meritocracy is restricted only to connected mayors, I interact GDP growthwith the connection variables. As reported in Table 2.9, the interaction coefficient is not signifi-cant. Hence, I conclude that my null result is not driven by meritocratic promotion being applieddifferentially to connected and unconnected mayors.2.6.2 PollutionAnother factor that could explain my null result is omitting variables that are used as promo-tion criteria. In particular, Zheng et al. (2014) finds that pollution reduction is correlated withpromotion for prefecture mayors over 2004-2009. My null result could be driven by pollution beingan omitted variable. Under this scenario, mayors are promoted meritocratically based on GDPgrowth, so long as they are also environmentally friendly.I test this hypothesis by interacting GDP growth with a pollution variable. I measure pollutionusing data on PM2.5 (from NASA) and industrial sulfur dioxide emissions (SO2, collected from theprovincial yearbooks). I calculate dummy variables for whether a mayor’s pollution is above theprovince-year median; I measure pollution using the growth rate as well as by taking the log, forboth PM2.5 and SO2. If only the environmentally-friendly mayors are promoted meritocratically,we should observe a negative coefficient on the interaction between growth and the above-medianpollution dummy.The results are presented in Tables 2.10 and 2.11. The interaction effects are nonsignificant forboth pollution variables, and for both the growth and log specifications. I conclude that meritocraticpromotion is not applied differentially to mayors based on their environmental quality.2.6.3 Corruption crackdownUpon taking office in late 2012, Xi Jinping launched an extensive corruption crackdown, arrest-ing thousands of officials, from low-level bureaucrats to Politburo members. Has this crackdownaffected the promotion tournament? If Hsieh et al (2019) are correct that China’s growth dependson crony capitalism, then we might expect the crackdown to upend meritocratic promotion. Inparticular, if mayors need to engage in corruption in order to boost growth, then the high-growthmayors will also be the corrupt officials targeted in the crackdown.There are two mechanisms through which the crackdown can generate a null result for meri-tocratic promotion. First, corruption is possibly an omitted variable, driving both GDP growthand arrests. If high-growth mayors are arrested, I will pick up a mechanically negative effect onpromotion, since by definition, being arrested means Promotion = 0. This negative effect couldmask a true positive effect.17Second, by deterring growth-boosting corruption, the crackdown would also hinder economicgrowth. If the government realizes that GDP growth is tightly linked to corruption, it may putless or even negative weight on growth in determining promotion. Hence, my null result couldbe explained by a structural break in the growth-promotion relationship in 2012, with a positivecorrelation before being cancelled out by a negative correlation afterwards. I test these hypothesesin Table 2.12 by controlling for arrests and interacting GDP growth with a post-crackdown dummy.I find that the mechanical effect of arrests is negligible. In my data, 35 mayors are arrested forcorruption while in office, making up 2% of all 1684 mayors, which is not large enough to sway themain result. As shown in Columns (1) and (2), controlling for arrests barely changes the coefficienton growth. Moreover, a t-test of average relative growth comparing arrested and non-arrestedmayors finds that arrested mayors actually have lower growth rates (although not statisticallydifferent). Hence, it is not the case that high-growth mayors are arrested for corruption. Oneinterpretation, consistent with Hsieh et al. (2019), is that the crackdown was not targeting growth-friendly corruption, which is still permitted by the regime, but rather growth-hindering corruption.Otherwise, this result casts some doubt on Hseih’s claim that cronyism is necessary for growth.In Columns (3) and (4) I test for a structural break in the effect of growth on promotion at thelaunch of the corruption crackdown. I find that the both the individual and interaction terms arenegative and nonsignificant, even controlling for arrests. So it is not the case that the governmentpromoted mayors meritocratically before the crackdown and nonmeritocratically afterwards. Hence,the corruption crackdown does not explain the null result for meritocratic promotion.2.7 ConclusionIn contrast to the literature, I find no evidence for meritocratic promotion of prefecture lead-ers. This null result is robust to many different specifications and variable definitions, and is notexplained by heterogeneous effects or omitted factors like political connections or the corruptioncrackdown. One explanation for this null result is that prefecture mayors are evaluated on manyfactors, such as party loyalty, environmental quality, and social policy, as well as economic growth,and hence the signal from GDP growth is too weak to detect empirically.The original motivation for the meritocracy literature was to provide an explanation for China’sincredible economic growth. But is meritocracy necessary for understanding how China couldsustain double-digit growth for three decades? After all, China had favorable conditions for growth:high levels of human capital, high state capacity, and political stability, to name a few. Perhapsstandard growth theory gives a sufficient explanation, without needing to appeal to the incentivesof politicians. Alternatively, it is possible that politicians were indeed incentivized to boost growth,but for the purpose of raising tax revenues rather than winning a promotion tournament. As arguedby Su et al. (2012), local governments targeted economic growth in order to make up for the revenueshortfall caused by the 1994 tax reform, which shifted revenues to the central government. I am18not taking a stand on whether these alternative explanations are correct. Instead, I merely wantto demonstrate that, as economists, our explanations for China’s growth remain strong even if wediscard the meritocracy hypothesis. I will revisit the question of meritocracy in China in Chapter3, where I find some evidence for meritocratic promotion at the county level.2.8 Tables and figuresTable 2.1: Summary statisticsmean min p50 max countAnnual GDP growth 0.11 -0.49 0.10 2.02 5640Average relative growth 0.00 -0.59 -0.00 1.62 5640Log GDP 6.37 1.18 6.40 10.02 5640Log population 5.74 2.00 5.85 7.27 5636Promotion 0.18 0.00 0.00 1.00 5640Age 49.97 26.00 50.00 61.00 5566Sex 0.07 0.00 0.00 1.00 5420Education 2.84 1.00 3.00 4.00 5329Tenure 2.56 1.00 2.00 14.00 5640Arrested 0.06 0.00 0.00 1.00 5285Home prefecture 0.11 0.00 0.00 1.00 5573Political connection 0.73 0.00 1.00 1.00 5628Observations 564019Table 2.2: No effect of GDP growth on promotionLPM Logit Ordered logit(1) (2) (3) (4) (5) (6) (7) (8) (9)GDP growth -0.034 -0.091 -0.060 -0.282 -0.890 -0.687 -0.044 -0.485 -0.164(0.085) (0.089) (0.108) (0.718) (0.845) (0.901) (0.672) (0.743) (0.848)Age 0.047∗ 0.056∗∗ 0.374 0.519∗∗ 0.548∗∗ 0.654∗∗∗(0.024) (0.025) (0.261) (0.246) (0.218) (0.217)Age squared -0.001∗∗ -0.001∗∗ -0.004 -0.005∗∗ -0.006∗∗∗ -0.007∗∗∗(0.000) (0.000) (0.003) (0.002) (0.002) (0.002)Sex 0.017 0.018 0.121 0.132 0.132 0.148(0.024) (0.024) (0.154) (0.154) (0.155) (0.154)Home prefecture -0.083∗∗∗ -0.065∗∗∗ -0.793∗∗∗ -0.600∗∗∗ -0.715∗∗∗ -0.572∗∗∗(0.018) (0.019) (0.178) (0.181) (0.161) (0.167)Connection -0.042∗∗ -0.041∗∗ -0.224 -0.223 -0.276∗ -0.277∗(0.020) (0.020) (0.156) (0.159) (0.154) (0.156)Initial GDP -0.017∗ -0.124 -0.097(0.009) (0.079) (0.079)Initial Population 0.018∗ 0.132 0.160∗(0.011) (0.090) (0.089)Observations 5640 5172 5141 4367 3954 3927 5658 5198 5173Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes Yes Yes Yes Yes Yes Yes YesMayor covariates No Yes Yes No Yes Yes No Yes YesPrefecture covariates No No Yes No No Yes No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDPgrowth is a mayor’s cumulative average relative growth rate over their term. Mayor covariates include dummy variablesfor tenure and education categories. Prefecture covariates includes dummy variables for prefecture type. Standard errors clusteredat the prefecture level in LPM, and at the province-year level in the logit and ordered logit models.20Figure 2.1: Robustness checks: linear probability model21Table 2.3: RegionsSoutheast Jiangsu Zhejiang Fujian Guangdong HainanSouthcentral Henan Hubei Hunan Anhui JiangxiNortheast Shandong Hebei Liaoning Jilin HeilongjiangNorthcentral Shanxi Inner MongoliaNorthwest Shaanxi Ningxia Gansu Qinghai XinjiangSouthwest Guangxi Guizhou Yunnan Sichuan TibetTable 2.4: ErasJiang Hu: I Hu: II Xi1998-2002 2003-2007 2008-2012 2013-201722Table 2.5: Heterogeneous effects by region(1) (2) (3)GDP growth 0.116 -0.263 -0.213(0.346) (0.478) (0.482)Growth × Northeast -0.252 0.057 -0.015(0.421) (0.535) (0.540)Growth × Northcentral -0.157 0.111 0.125(0.449) (0.547) (0.559)Growth × Northwest -0.215 0.152 0.134(0.379) (0.526) (0.530)Growth × Southwest -0.174 0.234 0.293(0.362) (0.482) (0.510)Growth × Southcentral -0.088 0.309 0.305(0.385) (0.513) (0.515)Observations 5640 5172 5141Adjusted R2 0.079 0.125 0.127Province-year FE Yes Yes YesMayor characteristics No Yes YesPrefecture characteristics No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Omitted group is Southeast. Regression model is asin Equation 2.1, with Growth interacted with region dum-mies. GDP growth is a mayor’s cumulative average rela-tive growth rate over their term. Mayor covariates includedummy variables for tenure and education categories. Pre-fecture covariates includes dummy variables for prefecturetype. Standard errors clustered at the prefecture level.23Table 2.6: Heterogeneous effects by era(1) (2) (3)GDP growth 0.101 0.013 0.031(0.179) (0.217) (0.220)Growth × Hu I era -0.110 -0.090 -0.053(0.184) (0.225) (0.247)Growth × Hu II era -0.087 0.079 0.120(0.253) (0.281) (0.287)Growth × Xi era -0.477 -0.443 -0.470(0.300) (0.320) (0.321)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor characteristics No No YesPrefecture characteristics No Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Omitted group is Jiang Zemin II era (1998-2002).Regression model is as in Equation 2.1, with Growth in-teracted with region dummies. GDP growth is a mayor’scumulative average relative growth rate over their term.Mayor covariates include dummy variables for tenureand education categories. Prefecture covariates includesdummy variables for prefecture type. Standard errors clus-tered at the prefecture level.Table 2.7: Summary stats: political connectionsmean min max countHometown (prefecture) 0.03 0 1 5571Hometown (province) 0.30 0 1 5573School 0.01 0 1 5516Patron 0.73 0 1 5626Observations 563824Table 2.8: Controlling for political connections(1) (2) (3) (4) (5)GDP growth -0.061 -0.060 -0.061 -0.071 -0.079(0.106) (0.107) (0.107) (0.107) (0.108)Hometown (prefecture) -0.010(0.029)Hometown (province) 0.022(0.015)School 0.024(0.040)Patron -0.042∗∗(0.020)Observations 5153 5153 5153 5142 5141Adjusted R2 0.125 0.125 0.125 0.126 0.126Province-year FE Yes Yes Yes Yes YesCovariates Yes Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Average growth is a mayor’s cumulative average relative growth rateover their term. Covariates include dummy variables for tenure, educationcategories, and prefecture type. Standard errors clustered at the prefecturelevel.Table 2.9: Interacting growth × connections(1) (2) (3) (4) (5)Baseline Pref. hometown Prov. hometown School PatronGDP growth -0.061 -0.067 0.041 -0.068 0.002(0.106) (0.099) (0.126) (0.107) (0.264)Connection -0.011 0.022 0.016 -0.042∗∗(0.029) (0.015) (0.044) (0.020)Connection × Growth 0.189 -0.326 -1.187 -0.102(0.907) (0.261) (2.109) (0.273)Observations 5153 5153 5153 5142 5141Adjusted R2 0.125 0.125 0.125 0.126 0.126Province-year FE Yes Yes Yes Yes YesCovariates Yes Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Average growth is a mayor’s cumulative average relative growth rate over their term. Co-variates include dummy variables for tenure, education categories, and prefecture type. Standarderrors clustered at the prefecture level.25Table 2.10: Pollution results: SO2(1) (2) (3) (4)Growth rate -0.093 -0.021 -0.103 -0.119(0.145) (0.192) (0.136) (0.182)SO2 growth > median -0.000 -0.000(0.012) (0.012)Growth × SO2 growth > median -0.152(0.284)Log SO2 > median -0.006 -0.006(0.012) (0.012)Growth × Log SO2 > median 0.029(0.269)Observations 3717 3717 3957 3957Adjusted R2 0.127 0.127 0.125 0.125Province-year FE Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Growth rate is a mayor’s cumulative average relative growth rate overtheir term. Covariates include a quadratic in age, dummy variables for sex,tenure, education categories, and home prefecture, as well as log initial GDPand population, and dummy variables for prefecture type. Standard errorsclustered at the prefecture level.Table 2.11: Pollution results: PM2.5(1) (2) (3) (4)Growth rate -0.042 -0.081 -0.051 -0.036(0.117) (0.171) (0.114) (0.153)PM2.5 growth > median -0.002 -0.002(0.010) (0.010)Growth × PM2.5 growth > median 0.078(0.211)Log PM2.5 > median -0.001 -0.001(0.011) (0.011)Growth × Log PM2.5 > median -0.032(0.220)Observations 4714 4714 4820 4820Adjusted R2 0.123 0.123 0.124 0.123Province-year FE Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Growth rate is a mayor’s cumulative average relative growth rate overtheir term. Covariates include a quadratic in age, dummy variables for sex,tenure, education categories, and home prefecture, as well as log initial GDPand population, and dummy variables for prefecture type. Standard errors clus-tered at the prefecture level.26Table 2.12: Corruption crackdown(1) (2) (3) (4)Growth rate -0.061 -0.064 -0.001 -0.006(0.106) (0.107) (0.113) (0.113)Arrest -0.270∗∗∗ -0.269∗∗∗(0.037) (0.037)Growth × Post -0.289 -0.279(0.256) (0.259)Observations 5153 5153 5153 5153Adjusted R2 0.125 0.128 0.125 0.128Province-year FE Yes Yes Yes YesCovariates Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Growth rate is a mayor’s cumulative average relativegrowth rate over their term. Arrest is a dummy variable formayors who were arrested while in office. Covariates include aquadratic in age, dummy variables for sex, tenure, education cat-egories, and home prefecture, as well as log initial GDP and pop-ulation, and dummy variables for prefecture type. Standard er-rors clustered at the prefecture level.27Chapter 3Reanalyzing the literature onmeritocratic promotion3.1 IntroductionIn Chapter 2, I found no evidence for meritocratic promotion of prefecture leaders. And yet,there are many papers in the literature that claim to provide evidence for meritocracy at theprefecture level. How can this tension be resolved? In this chapter, I revisit five papers from thisliterature. Digging into these papers, I find that their prefecture results are not robust to reasonablespecification choices, and in one case, are due to possible data errors. In each case, I find that thepaper does not provide robust evidence for meritocratic promotion. I conclude that my results inChapter 2 are sound, and that the papers in this literature contain flaws.To preview my results, I replicate papers published in the Journal of Economic Growth, theEconomic Journal, the Quarterly Journal of Economics, Comparative Political Studies, as well asa working paper.31 I find that the results in four papers (JEG, EJ, CPS, WP) are replicable usingtheir own data and code, but are not robust to different specifications. I find that the results inthe final paper (QJE) are possibly due to data errors. Using Clemens (2017)’s terminology, I amperforming a reanalysis in the former cases, and a verification in the latter case.32Lastly, I re-examine the evidence for meritocracy at the province and county levels. At theprovince level, a new paper (Sheng, 2020) claims to find evidence for meritocratic promotion onlyfor provincial governors during the Jiang Zemin era (1990-2002). I test this hypothesis using thedata from Jia et al. (2015) and find no such effect. For county leaders, the two papers on county-level politicians (Chen and Kung, 2016; Landry et al., 2018) use non-standard specifications, so Ire-analyze their data using my preferred specification: regressing an annual promotion variable oncumulative average relative GDP growth. In this case I find suggestive evidence for meritocracybeing implemented for county leaders. I conclude by proposing a model of meritocracy wherecounty-level promotion tournaments provide a causal explanation for China’s economic growth, by31Appendix Table B.1 presents a summary of the sample and methods used in each paper.32Clemens distinguishes between replication and robustness. Replication includes verification (same specification,same population, and the same sample) and reproduction (same specification, same population, and a differentsample). Robustness includes reanalysis (different specification, same population, and possibly the same sample) andextension (same specification, different population, and a different sample). In my case, I am using the same data asthe original paper, but changing the specification. For the QJE paper, data errors count as a failed verification.28incentivizing county leaders and selecting higher-level leaders based on ability to grow the economy.3.2 Yao and Zhang (2015)Yao and Zhang (2015), published in the Journal of Economic Growth, was the first paper tostudy meritocratic promotion at the prefecture level in China. They apply the AKM approach toleaders and cities (instead of workers and firms), using leaders that move across cities to identifyleader ability to boost GDP growth. The main contribution is estimating the effect of leader abilityon promotion.Leader effects are estimated in a three-way fixed-effect model, along with year and city fixedeffects:yijt = βXijt + θi + ψj + γt + ijt. (3.1)Here yijt is real GDP growth in city j in year t, Xijt is time-varying controls, θi is leader i’s fixedeffect, and ψj and γt are city and year fixed effects. When using the largest sample connected bymovers, all three fixed effects can be identified in a regression of GDP growth on the fixed effects.Note that this paper pools prefecture mayors and secretaries, which allows for a larger maximalconnected set, but also gives up the ability to test for heterogeneity in meritocratic promotion acrossmayors and secretaries. Note also that restricting to the largest connected set means potentiallylosing external validity, if there are heterogeneous effects by membership in this connected set.The authors estimate the effect of leader ability on promotion in the following model:pijt = αθi + δZijt + νk + ηt + uijt. (3.2)Here pijt is either a dummy or a categorical variable, Zijt is control variables, and νk and ηt areprovince and year fixed effects. I directly replicate their Table 4 in Table 3.1 below. I make a fewchanges to their code. First, I cluster standard errors at the prefecture level; the original paperdid not cluster. Second, the original paper made a coding error in the Age > Threshold variable.Specifically, the authors neglected the fact that Stata’s gen function treats missing observations asinfinite, so observations with a missing age variable are coded as being above the threshold. I correctthis error, which reduces the sample size in Columns 3-6 to match that in Columns 1-2 (as thelatter columns automatically exclude the missing observations). Despite these changes, the resultsare almost identical. For example, the original coefficient on Leader effect× (Age > Threshold) inColumn 5 is 0.291∗∗∗, while mine is 0.311∗∗∗.They find no average correlation between leader effects and promotion, in either the LPM orordered probit models (Column 1 in Tables 4 and 5).33 This is consistent with my finding inChapter 2 that China does not promote prefecture leaders meritocratically (on the basis of GDP33Their original Tables 4-5 are presented as Appendix Figures B.1-B.4.29growth). Despite finding no average effect, the authors do not frame their paper as contradictingthe literature.34 Moreover, this paper is cited in the literature as supporting the meritocracyhypothesis.35This is because the authors further test for an interaction between leader ability and age,reporting a positive interaction effect that is significant at the 5% level. To narrow in on thisresult, they test for a series of interactions with indicator variables for age being above a threshold(from 49 to 52), finding that the effect of leader ability on promotion is strongest for leaders olderthan 51. They conclude that leader ability matters for older politicians, because more years ofexperience produces a clearer signal of ability.This result is consistent with a limited promotion tournament, where the Organization Depart-ment promotes older leaders based on their (lifetime) ability to boost growth (because older leadershave clearer signals of ability), but applies different promotion criteria to younger leaders (whosesignals are too weak to detect). But this limited model contradicts the usual characterization ofChina’s promotion tournament as including all leaders, irrespective of age: in each province, lead-ers compete to boost GDP growth, and the winners (with the highest growth) are rewarded withpromotion.Moreover, half of all promotions occur for leaders younger than 51. If the Organization Depart-ment cannot measure ability for these young leaders, what criteria does it use to promote them?Furthermore, recall that the original motivation was to explain China’s rapid growth. The incen-tives generated by this limited tournament are weaker, since the reward is only applied later in life;if young leaders are impatient, they will discount this future reward and hence put less effort intoboosting growth. The limited tournament model thus has less explanatory power.36 Given thesedifferences in interpretation, it is not clear why this paper has been cited without qualification asevidence for meritocratic promotion, when it supports only a limited promotion tournament.Besides these problems in interpretation, I also find issues in the paper’s empirical results. Whenestimating leader effects, the authors regress GDP growth on the three fixed effects as well as threecovariates: initial city GDP per capita (by leader term), annual city population, and the annual34“We also improve on the existing literature on the promotion tournament in China. Using the leader effectestimated for a leaders contribution to local growth as the predictor for his or her promotion, we refine the approachof earlier studies.” (Yao and Zhang 2015, p.430)35Chen and Kung (2016): “those who are able to grow their local economies the fastest will be rewarded withpromotion to higher levels within the Communist hierarchy [...] Empirical evidence has indeed shown a strongassociation between GDP growth and promotion ([...] Yao and Zhang, 2015)”.Yao (2018): “Some studies have found that officials who perform better during their term of office are promotedmore easily ([...] Yao and Zhang 2015)”.Li et al. (2019): “the promotion of Chinese local officials is linked to economic growth in their jurisdictions. Thisstrong linkage between the private interests of local officials and regional economic development thereby triggers anintensive tournament competition ([...] Yao and Zhang, 2015).”36Another explanation suggested by the authors is that competition in the promotion tournament is more intensefor older leaders, which increases the importance of ability in determining promotions. However, it is not clearwhy competition should vary with leader age, nor why more intense competition should increase the OrganizationDepartment’s weight on ability.30provincial inflation rate. We might worry that small cities mechanically grow faster, since theystart from a lower base. But since the model includes city effects, level differences in growth ratesare not an issue. A second worry is that the variance of idiosyncratic shocks to growth is correlatedwith city size. Since growth shocks could affect promotion outcomes, it makes sense to control forinitial GDP by term. However, it is not clear why population and inflation should be included.The authors mention that labor migration can drive GDP growth (p.413), but a leader’s policiesaffect migration, so population is plausibly a collider or ‘bad control’, if leader ability affects growththrough good policies that increase migration. The authors provide no justification for includinginflation, which is odd because the dependent variable (real per capita GDP growth) is alreadyexpressed in real (rather than nominal) terms.While the authors perform multiple robustness checks after they have estimated the leadereffects, they do not apply robustness checks to the estimation of the leader effects itself. Given thelack of a strong justification for including population and inflation as covariates, I re-estimate theleader effects controlling only for initial GDP. Using these new leader effects, I then re-estimatetheir Table 4, which was directly replicated above. The results of my reanalysis are presented inTable 3.2.While the average effect of leader effects (Column 1) is quite similar to the original (0.033 vs.0.029), I find no statistically significant interaction effect with age (Column 2). The signs remainunchanged, but the magnitude of the coefficients drops by half, and the results are nonsignificant.Turning to the age threshold results (Columns 3-6), I find that the coefficient on Leader effect ×(Age > Threshold) remains statistically significant only for the age 51 threshold, though at the 5%level instead of the original 1% (Column 5). These coefficients are smaller by one-third to one-half,compared to the original regressions.I find similar results when reanalyzing the other specifications (LPM and ordered probit in bothsingle- and multiple-equation models); see Appendix Tables B.2 – B.4. The interaction effect withAge becomes nonsignificant, and out of the threshold interactions, only the age 51 threshold retainssignificance (at the 5% level).Since dropping population and inflation when estimating leader effects seems like an innocuouschange, I conclude that the reported interaction effect is not robust.37 This is an innovative,insightful38, and well-written paper. However, the results do not support a model of meritocraticpromotion for prefecture leaders in China.37In unreported results, I find that controlling for both initial GDP and initial population (rather than annualpopulation) again leads to a nonsignificant interaction. However, the replication files are missing data on a leader’sfirst year in office, so this estimate uses a smaller sample size than in the original regressions.38For example, they note that almost all members of the Politburo Standing Committee (PSC) have worked in asmall set of advanced provinces and big cities that benefited from special economic policies. Hence, defining politicalconnections based on shared work experience with current PSC members may result in a spurious positive correlationbetween connections and promotion. (p.421) This insight is the basis of Fisman et al. (2020).313.3 Li et al. (2019)Li et al. (2019), published in the Economic Journal, studies GDP growth targets and promotiontournaments in China. They note that targets are higher at lower levels of the administration; forexample, prefectures set higher targets than do provinces. Their explanation is that the numberof jurisdictions competing in each promotion tournament is decreasing as one moves down thehierarchy, which increases the probability of a leader winning the tournament. As a consequence,leaders exert more effort, and higher-level governments can set higher growth targets while satisfyingthe leaders’ participation constraint.As part of their model, they assume that promotion is meritocratic: performance (measured byGDP growth) increases the probability of promotion, consistent with the literature. Further, theyreport an original result: the effect of performance on promotion is increasing in the growth targetfaced. That is, a one percentage-point increase in growth will increase a mayor’s P(promotion) bya larger amount when the provincial target is higher, relative to when the target is lower.This result seems naturally testable by interacting Growth×Target in a panel regression, witha predicted positive coefficient on the interaction term. However, the authors argue that OLS isinvalid, instead reporting results based on MLE where promotion is determined by a contest successfunction. Why does OLS not apply? “Standard linear regression does not work here partly becausepromotion is determined by local officials own growth rates as well as by the growth rates of theircompetitors. The nonlinearity of the promotion function is another factor that invalidates the OLSestimation.” (p.2906)But these do not seem to be problems for OLS. First, as is standard in this literature, thepromotion tournament can be captured by using prefecture growth rates relative to the annualprovincial growth rate. Second, OLS is the best linear approximation to a nonlinear conditionalexpectation function. So if there is a positive nonlinear relationship between promotion and growth,we should be expect that it will be detected by OLS. Given the lack of justification for omittingresults from linear regression, I will test for an interaction effect between growth and the growthtarget using a linear probability model and logistic regression.First, I present the original Li et al. Table 5 results in Figure 3.1. This table shows MLEestimates of the following log-likelihood:logL =1T∑i,t(ditlog(pit) + (1− dit)log(1− pit)).Here dit is in indicator for promotion, and pit is the promotion probability defined by:pit =g(yit, y¯t, xit)∑j g(yjt, y¯t, xjt)).In this equation, g is a linear score function, yit is leader i’s GDP growth rate, y¯t is the growth32target set by the upper-level government, and xit contains control variables. The score functionhas the formg(yit, y¯t, xit) = 1 + α1yit + α2y¯t + xitβ.The model in Li et al. assumes that α1 > 0 and α2 < 0, corresponding to the assumptions ofmeritocratic promotion and complementarity between growth targets and the responsiveness ofpromotion to GDP growth. As we can see in Figure 3.1, the coefficient on GDP growth is positive,while the coefficient on the growth target faced is negative, whether using annual or cumulativegrowth.Next, I reanalyze the Li et al. hypothesis using an interaction effect and OLS. To capture theidea that the effect of GDP growth on promotion is increasing in the growth target faced, I estimatethe following model:Promotionijpt = β1Growthijpt + β2Growthijpt × Targetpt + λXijpt + ijpt. (3.3)In this setup, the Li et al. assumptions are formulated as β1 > 0 (in a model without the interactionterm) and β2 > 0: growth directly increases the probability of promotion, and the effect of growthon promotion is increasing in the growth target faced.The results are presented in Table 3.3, which replicates columns (1) and (3) in Table 5 of Li etal. (2019). First, I test the generic meritocracy hypothesis in the first and third columns, omittingthe interaction term. I find that GDP growth has no average effect on promotion, either as annualor average cumulative growth. This confirms my null result from Chapter 2. The second and fourthcolumns find positive interaction effects between realized growth and the growth target faced, butthese are not statistically significant.39 I find similar results when using logistic regression (seeAppendix Table B.5). In unreported results, I include separate province and year fixed effects(instead of province-year fixed effects), and find similar nonsignificance. Hence, while the authorsfind that the corresponding results are statistically significant when using MLE, they are not robustto linear specifications. A further worry is that the panel is somewhat unbalanced (due to missingdata on growth targets). As shown in Appendix Figure B.9, the sample size varies moderately fromyear to year, possibly leading to unrepresentative estimates.While Li et al. (2019) is an interesting extension to the promotion literature and offers aninsightful analysis of GDP growth targets as a function of the number of contestants per promotiontournament, it does not provide robust evidence for meritocratic promotion of prefecture leaders.39Note that the growth target (set by the provicial government for prefecture leaders to achieve) varies at theprovince-year level, and hence is collinear with the province-year fixed effect.333.4 Chen and Kung (2019)Chen and Kung (2019), published in the Quarterly Journal of Economics, studies land cor-ruption in China, with secondary results on meritocratic promotion. The main result is that localpoliticians provide price discounts on land sales to firms connected to Politburo members, and theselocal politicians are in turn rewarded with promotion up the bureaucratic ladder.For provincial leaders, they find a strong effect of land sales on promotion for secretaries, butnot for governors. In contrast, GDP growth strongly predicts promotion for governors, but notsecretaries. They conclude that “the governor has to rely on himself for promotion, specifically byimproving economic performance or GDP growth in his jurisdiction [...] only the provincial partysecretaries are being rewarded for their wheeling and dealing”.They find similar results at the prefecture level: land deals predict promotion for secretaries, butnot for mayors, while GDP growth predicts promotion for mayors, but not for secretaries. Overall,this supports the model of party secretaries being responsible for social policy, while governors (andmayors) are in charge of the economy, with performance on these tasks determining promotion.40Thus, at both province and prefecture levels, government leaders (governors and mayors) competein a promotion tournament based on GDP growth, while party secretaries do not.41However, Chen and Kung (2019)’s results for prefecture mayors are questionable, because theirpromotion data seems to contain data-entry errors. In my data, the annual promotion rate variesfrom 5 to 30% (peaking in Congress years), while the Chen and Kung (2019) data never exceeds15% and has six years where the promotion rate is less than 2%. Figure 3.2 compares the annualpromotion rate from Chen and Kung to my own data as well as the data from Yao and Zhang(2015) and Li et al. (2019), where each paper uses a binary promotion variable. While the latterthree sources broadly agree on the promotion rate, the Chen and Kung data is an outlier.Neither the text nor the appendix in Chen and Kung (2019) discusses the data sources orspecifically how the promotion variable was defined (e.g., what differentiates a transfer from apromotion), so it is not clear why their promotion rate differs so much from the rest of the literature.Without an explanation, this disagreement should lead us to be cautious in interpreting their results.Furthermore, upon investigating this discrepancy, I discovered apparent data errors in theirpromotion variable. The annual promotion variable is defined to be 1 in the year a mayor ispromoted, and 0 otherwise. However, out of the 201 cases with Promotion = 1, 124 occur beforethe mayor’s last year in office (with the remaining 77 cases occuring in the last year). Moreover,this variable is equal to 1 multiple times per spell in 4% of leader spells. Table 3.4 calculates thesum of the promotion variable at the spell level. Out of 1216 spells, 51 (=16+12+18+5) have40Jia (2017) makes a similar point: “[Provincial secretaries’] major responsibilities include the implementation ofthe central government policies and social stability whereas governors’ key duty is to promote growth.” p.12 fn.1541Note that the authors find a positive correlation between growth and promotion while using annual GDP growthrather than average cumulative growth; they also do not control for tenure, which in my data has a strong positivecorrelation with promotion.34Promotion = 1 more than once per spell. For example, consider a mayor who is in office for fiveyears and then promoted; the promotion variable should be 0 in the first four years, then 1 inthe final year. However, the Chen and Kung data has spells where the promotion variable is, forexample, 0 in the first two years, and 1 in the final three years.Since the replication files include prefecture- but not mayor-level data, this error is not easy todetect; a sequence of 1’s could reflect multiple mayors being promoted in their first year, ratherthan the same mayor being coded as promoted multiple times in the same spell. I obtained theraw mayor data from James Kung, and used it to generate a corrected annual promotion variable,which is 1 only in a mayor’s final year in office (when the mayor is promoted). This data-codingerror more than doubles the number of promotions. Figure 3.3 shows the original and correcteddata, along with my promotion data. Since the Chen and Kung promotion rate is smaller than therest of the literature, fixing the data errors in fact makes the disagreement with the literature evenmore pronounced.Next I test whether the Chen and Kung meritocracy result for prefecture mayors (reportedin their Table IX) is driven by their promotion variable.42 First, using the corrected promotionvariable, I find that the results are mostly consistent, with a positive p < 0.01 coefficient on GDPgrowth in each regression (see Appendix Table B.7). So the meritocratic effect found in Chen andKung (2019) is not driven by the particular data error discussed above. However, it could still bedriven by their promotion definition, which, as shown in Figures 3.2 and 3.3, differs sharply fromthe rest of the literature.Hence, I re-estimate the effect of GDP growth on promotion with my own promotion data.43To focus on the effect of GDP growth, I omit all politician-defined covariates and include only theprefecture covariates (tax revenue growth rate, log GDP per capita, and log population). This isto avoid issues stemming from possible disagreements over the identity of mayor i in prefecture pin year t.44 I also cluster standard errors at the prefecture level, because the original paper did notcluster. Finally, I restrict the sample size to match my promotion data; my data is missing a fewprefectures in Tibet, which reduces the sample size from the original 2569 to 2549.I estimate the following regression:yijpt = β ·Growthijpt + δXjpt + θt + γj + ijpt. (3.4)42I provide a direct replication of Table IX in Appendix Table B.6, where I perfectly reproduce the results in theoriginal paper.43Table IX estimates the effect of land sales, political connections, and GDP growth on promotion for prefecturemayors over 2004-2014. However, there are some discrepancies between the published table and the replication code.First, the table reports using data from 2004-2016, but the replication files only include data over 2004-2014. Second,while the authors report using robust standard errors, this is not implemented in the replication code. Third, thetable reports using province fixed effects, but the replication code actually uses prefecture fixed effects.44For example, if my data has mayor A in office, while their data records mayor B, then the age, education, andpolitical connection variables will disagree.35The dependent variable is an ordered or dummy promotion variable, and prefecture covariates areincluded in X. As in the original specification, I include year (θt) and prefecture (γj) fixed effects.Columns 1-2 of Table 3.5 present ordered probit and LPM results using the original Chen andKung promotion data. Despite the above changes in specification and sample, the results are nearlyidentical to those in the original paper. For example, the Chen and Kung (2019) LPM coefficienton GDP growth is 0.365∗∗∗, compared to 0.379∗∗∗ here (Column 2). Hence, the meritocratic effectreported in the original paper is not driven by politician covariates, small changes in the sample,or clustering standard errors.To test whether the promotion variable is key to their results, I perform the same analysisusing my own promotion data in Columns 3-4 of Table 3.5. I find that the coefficient on GDPgrowth is now negative and nonsignificant. This nonsignificance holds over three other versions ofmy promotion variable (using different definitions as in Chapter 2), as I show in Appendix TablesB.8 - B.10.Hence, given these results and the disagreements over the promotion variable between Chenand Kung and the rest of the literature, I conclude that the positive growth-promotion correlationfor prefecture mayors found in Chen and Kung (2019) was an artifact of their potentially flawedpromotion variable. While offering an astute analysis of land corruption, Chen and Kung (2019)does not provide robust evidence that prefecture mayors are promoted meritocratically on the basisof GDP growth.3.5 Landry et al. (2018)Landry et al. (2018), published in Comparative Political Studies, tested the meritocratic pro-motion hypothesis at the provincial, prefecture, and county levels over 1999-2007. They find strongevidence for meritocracy at the county level, but not at the prefecture or province levels. They alsofind that politicial connections (defined as the ‘patron connection’ from Chapter 2) affect promotionmost at the provincial level. (Following Jia et al. (2015), they also test for an interaction effectbetween growth and connections, but find no significant results.) They interpret their findings asdemonstrating the loyalty-competence tradeoff faced by Chinese officials: county leaders are se-lected based on competence, since they do not pose a threat to central government officials; whileprefecture and provincial leaders are selected based on connections and other non-performance fac-tors, since competent but disloyal leaders, if promoted, could threaten the incumbent elites. Thus,the Chinese system can select for leaders who are both competent and loyal.This paper follows the literature in using a linear probability model to estimate the effect of36relative GDP growth on promotion.45 In particular, they estimate the following model:yijpt = β1Growthijpt + β2Connectionit+β3Growthijpt × Connectionit +Xijpt + δp + γt + ijpt.(3.5)However, they depart from the literature in using spell-level data rather than a prefecture-yearpanel. Hence, they regress a promotion dummy on a leader’s average GDP growth, while theusual approach is to calculate a leader’s cumulative average growth rate over their tenure. WhileLandry et al.’s null prefecture results are consistent with mine, for the sake of robustness I performa reanalysis using a different specification. Next I re-analyze their Tables 5-6 using cumulativeaverage growth in a jurisdiction-year panel instead of spell-level data; this includes results forprovince-, prefecture-, and county-level politicians.46The results are presented in Tables 3.6 - 3.8. I find similar results, but they do not support theoverall narrative in Landry et al. (2018). For provincial leaders, Landry et al. (2018) reported noeffect of GDP growth for secretaries, and a strong negative effect for governors. They also foundno effect of connections for secretaries, and a weak positive effect for governors. In my replication,I find similar null effects for secretaries, but I fail to match their governor results: using annualdata, the strong negative effect of GDP growth becomes a precise zero, and while I find a positivecorrelation with connections, it is one-quarter the size and not statistically significant.At the prefecture level, I confirm their original result of no growth-promotion correlation foreither mayors or secretaries, which is again consistent with my Chapter 2 results. I find a verystrong negative effect of connections on promotion, that disappears (entirely for secretaries andmostly for mayors) upon controlling for politician characteristics. This is because the connectionvariable is strongly correlated with tenure, and politicians are less likely to be promoted early intheir term. (Note that in Chapter 2 I also found a weak negative effect of patron connections formayors.)I find somewhat consistent evidence that county leaders are promoted meritocratically. I finda very weak effect for secretaries, much smaller than in the original paper (0.008∗ compared to0.044∗∗∗). I find a slightly larger effect size for mayors (0.012∗∗ compared to the original 0.037∗∗∗),but this average is masked by heterogeniety via a negative interaction with connections, contra-dicting the narrative from Jia et al. (2015) of connections being complementary to performance.Furthermore, while the original results suggest a weak positive effect of political connections forcounty mayors, I find a nonsignificant effect (after controlling for tenure, as with the prefectureresults).Thus, while the data in Landry et al. (2018) weakly supports the hypothesis of county-levelmeritocracy, it does not fit a simple model of a loyalty-competence tradeoff. Political connections45The paper also tests for meritocracy using the growth rate of tax revenue as a measure of performance. Givenmy focus on GDP growth, I ignore these results here.46Appendix Tables B.11-B.13 provide direct replications of the original results.37do not become more important at higher levels; instead, they either have no effect on promotion(for county and province leaders, and prefecture secretaries) or have a weak negative effect (forprefecture mayors). However, the result of meritocratic promotion for county leaders does seemsomewhat robust, as I find similar results when using annual panel data.3.6 Lorentzen and Lu (2018)Lorentzen and Lu (working paper, 2018) is a recent contribution to the meritocracy literature.Drawing on the 2012 corruption crackdown, one section of their paper focuses on three high-ranking“Tigers” who were arrested for corruption. In particular, they study whether leaders were promotednon-meritocratically in the provinces associated with these Tigers during the years preceding thecrackdown.47 If true, a natural conclusion is that the corruption crackdown was motivated by actualcorrupt behavior (rather than merely being a power grab by Xi Jinping).The paper uses data on prefecture mayors and party secretaries over 2006-2012. In contrast tomy preferred specification with annual data on cumulative average GDP growth, it uses spell-leveldata and average growth. Further, it restricts the sample to leaders with spells beginning after2005 and ending before 2013. The authors run the following linear probability model48 :yijp = β1 ·Growthijp + β2 ·Growthijp × Tigerp + δXjp + θZijp + γp + ijp. (3.6)Here the dependent variable is a promotion dummy, Tigerp is a dummy for Shanxi, Jiangxi,and Sichuan, Xjp is prefecture characteristics, Zijp is individual characteristics, and γp is a provincefixed effect. The authors find that β1 > 0 and β2 < 0, with statistical significance at the 5% or 10%level.49 Given that the Tiger provinces were the ones where high-ranking officials were arrested,this result supports the hypothesis that promotion was non-meritocratic in the Tiger provinces andmeritocratic everywhere else.Since this paper is still unpublished, there is no replication data that I can use to re-analyze itsresults. But I can test if its results are robust to using my own data (on prefecture mayors) andpreferred specification. First, I run a similar regression using spell-level data and province fixedeffects, while restricting the sample to 2006-2012 and using only leaders with spells beginning after2005 and ending before 2013. As in my main results from Chapter 2, I add in leader and prefecturecovariates in separate columns.47The three Tigers and their associated provinces are Su Rong (Jiangxi), Zhou Yongkang (Sichuan), and Ling Jihua(Shanxi).48The paper also includes interactions between Tiger province and various other criteria for meritocratic promotion:experience in the provincial General Office, experience in other provincial departments, membership in the provincialCommunist Youth League, as well as measures of political connections (shared college, hometown, and work history).Given my focus on GDP growth, I omit these variables here. In unreported results, I find no change when alsocontrolling for Connections × Tiger province, using my own political connections variable.49Their Table 4 is presented as Appendix Figure B.10.38Table 3.9 presents my replication of the results from Table 4 of Lorentzen and Lu (2018). Column(3) contains my preferred specification, including leader and prefecture covariates. I find that β1and β2 are always nonsignificant, and do not have the expected signs.50 Since using spell-level datadoes not use annual variation and results in a small sample size (and large standard errors on theinteraction term), I also test the ‘Tiger province’ hypothesis using annual data and my specificationfrom Chapter 2 (with cumulative average GDP growth as the independent variable). The results arepresented in Appendix Table B.17, where I again find nonsignificant estimates of β1 and β2. Hence,my reanalysis of Lorentzen and Lu (2018) does not confirm their results. This could be drivenby differing definitions of promotion, different control variables, or different samples. Without theoriginal data, I cannot draw any firm conclusions about this disagreement.Overall, I am not able to find evidence that the promotion of prefecture mayors was nonmeri-tocratic in Shanxi, Jiangxi, and Sichuan (and meritocratic elsewhere) prior to the 2012 corruptioncrackdown.3.7 Historical meritocracy for provincial leaders?In a forthcoming paper, Sheng (2020) finds that meritocratic promotion was implemented forprovincial governors only during the Jiang Zemin era (1990-2002), and never for provincial sec-retaries. Sheng argues that Deng Xioping’s 1992 “southern tour” solidified political support foreconomic reform, and in response Jiang Zemin pushed for liberalization and economic growth,ostensibly using meritocratic promotion of governors to achieve this goal. Sheng writes that “aclear-cut policy preference [by the central leadership] for economic growth per se seemed mostdiscernable in the years presided over by Jiang Zemin, but largely absent in the other years due toeither lack of elite policy unity or doubts over the wisdom of inordinate reliance on GDP growth.”Hence, we should expect to find a correlation between growth and promotion only for governors,and only during the Jiang Zemin era.Here I test this finding by replicating it using the data from Jia et al. (2015). There are severaldifferences between the datasets. This dataset has a smaller sample, from 1993-2009, so I can onlytest for parts of the Jiang Zemin and Hu Jintao eras. Jia et al. (2015) measures GDP growth bysubtracting the national average, then calculating the cumulative average over a leader’s term. Incontrast, Sheng (2020) does the same but additionally subtracts the average of provincial growthtaken over all years prior to the year a leader takes office; this is to capture whether a leader’sgrowth performance is superior to their predecessors. Furthermore, Sheng (2020) presents resultsfrom an ordered probit model. Since the promotion variable in Jia et al. (2015) is binary, I canonly run linear probability and probit models. Finally, the papers have different control variables,as well as different definitions of promotion.50I repeat the same analysis using different promotion definitions in Appendix Tables B.14 – B.16.39With these caveats in mind, I replicate Table 2 from Sheng (2020) in Table 3.10 below. Tomimic Sheng’s results, I estimate linear probability models separately by governors and secretaries,as well as by era.51 In contrast to Sheng’s results, I find no positive and statistically significanteffect for governors during the Jiang era. This null result may be explained by differences fromSheng (2020) in model specification, control variables, or sample periods. Future research shouldinvestigate which factors are driving the disagreement.3.8 Meritocracy for county leaders?Meritocratic promotion has been tested at the county level by two papers. Chen and Kung(2016) studies county secretaries over 1999-2008, and Landry et al. (2018) studies both mayors andsecretaries over 1999-2007.Chen and Kung (2016) analyzes the effect of land revenues on promotion. Here, I use theirdata to test for meritocratic promotion based on GDP growth. The original paper uses the annualgrowth rate of GDP per capita as the independent variable in linear probability and ordered logitmodels. I construct my preferred growth variable, the cumulative average of relative growth over apolitician’s tenure (relative to the prefecture average). This variable better captures the promotiontournament, where politicians are evaluated on their overall relative performance, rather than theirgrowth rate in any one year. I omit the land revenue variables used in the original paper. Myresults are in Table 3.11. I find a positive coefficient on GDP growth, which is robust acrossmultiple specifications.I analyze the Landry et al. (2018) data in Table 3.12. The coefficient on Growth is statisticallysignificant with no controls, but shrinks in magnitude when controlling for politician and countycharacteristics. Since they use GDP measured in standard deviations, but do not report summarystatistics on GDP growth, I use the standard deviation (0.154) from Chen and Kung (2016) tonormalize. The effect for secretaries is 0.008∗/0.154 = 0.052∗, and the effect for mayors is the same,but nonsignificant. Comparing to the Chen and Kung (2016) secretary results from the LPM, wesee that the coefficients are similar (0.071∗∗ vs. 0.052∗). Some difference in coefficients is expected,as the regressions use different control variables and promotion definitions.52 Despite this slightdisagreement, I conclude that there is some evidence for meritocracy at the county level.To further test for consistency across datasets, I test for heterogeneous effects over time. Specif-ically, I split the sample into eras by General Secretary: Jiang Zemin (1999-2002) and Hu Jintao(2003-2008). The results for Chen and Kung (2016) are presented in Columns (4) and (8) of Table3.11. I find a positive interaction effect (statistically significant only in the logit specification),indicating that meritocracy was stronger during the Hu era.51I attempted to estimate probit and logit models, but found that they did not converge, due to small sample size.52In the estimation samples, Chen and Kung (2016) has a promotion rate of 8.95% while Landry et al. (2018) hasa rate of 13.5%.40The results using the Landry et al. (2018) data are in Columns (3) and (6) in Table 3.12.I again normalize using the standard deviation from Chen and Kung (2016). The Landry et al.(2018) interaction effect for secretaries is 0.012/0.154 = 0.078, somewhat close to the Chen andKung (2016) LPM coefficient of 0.05 (although neither are statistically significant). I take thisagreement as further evidence that the datasets are similar, and that there is a meritocratic pro-motion signal to be detected. The interaction effect for mayors is negative with similar magnitude(−0.011/0.154 = −0.071), though nonsignificant, indicating that mayors and secretaries were pos-sibly treated differently during the Hu era.Overall, I take these results as suggestive evidence for meritocratic promotion of county lead-ers. However, we should wait to see additional robustness checks before drawing firm conclusions.For example, future work should extend the sample period beyond 1999-2008, as well as test forrobustness to different definitions of promotion.3.9 ConclusionThe best-published papers studying meritocracy at the prefecture level do not provide robustevidence that prefecture leaders are promoted based on their performance in growing GDP. Mynull result in Chapter 2 is not contradicted by the literature, since the results in the literature arenot robust to reasonable specification changes. Overall, I conclude that meritocratic promotion,at least at the prefecture level, does not explain China’s rapid economic growth. However, we sawthat county-level leaders do appear to be promoted meritocratically, using data from Chen andKung (2016) and Landry et al. (2018). Hence, it is possible that meritocracy does exist in China,but only for county leaders.So how should we think about meritocracy in China? Despite the mixed evidence for meri-tocratic promotion at the province and prefecture levels, it is still plausible that meritocracy hascontributed to China’s growth. County leaders are promoted meritocratically, directly incentivizingthem to boost GDP growth. In particular, the high-ability county leaders are promoted to pre-fecture positions. But since prefecture leaders then consist only of high-ability leaders, there isn’tenough variation in ability to implement a prefecture-level promotion tournament based on GDPgrowth. In other words, range restriction prevents the Organization Department from implement-ing meritocratic promotion above the county level. Running a successful county-level tournamentprecludes prefecture and provincial tournaments. Hence, the Organization Department must useother criteria in determining promotions of prefecture and provincial leaders.53Thus, county leaders are continuously incentivized to boost economic growth, and only leaders53However, as we have seen in my replication of Landry et al. (2018), it is not the case that higher-level leadersare promoted based on political connections, as in a simple model of a competence-loyalty tradeoff. Furthermore, asdiscussed in Chapter 2, the provincial literature finds inconsistent results for the effect of political connections. Shihet al. (2012) and Jia et al. (2015) provide evidence for a positive effect, while Fisman et al. (2020) finds a negativeeffect.41with demonstrated ability in this task are promoted to prefecture and provincial positions. Whilethey are not directly incentivized, these higher-level leaders are selected based on their abilityto grow the economy, and they supervise the county leaders in their jurisdiction. We can thinkof this as a version of partial meritocracy, in contrast to a ‘maximal’ version where leaders atall levels are incentivized through promotion tournaments. While the maximal version providesstronger incentives for boosting GDP growth, the partial version does generate some incentives aswell. Hence, it seems reasonable to conclude that, meritocracy in fact does partly explain China’seconomic growth, giving an answer to the initial question that motivated these two chapters.423.10 Tables and figures43Table 3.1: Direct replication of Table 4, Yao and Zhang (2015)(1) (2) (3) (4) (5) (6)Threshold: 49 Threshold: 50 Threshold: 51 Threshold: 52Leader effect 0.029 -1.262∗∗ -0.107 -0.072 -0.113 -0.039(0.049) (0.597) (0.080) (0.076) (0.070) (0.066)Leader effect × Age 0.026∗∗(0.012)Age -0.006∗∗∗ -0.006∗∗∗(0.001) (0.001)Provincial experience 0.051∗∗∗ 0.053∗∗∗ 0.052∗∗∗ 0.053∗∗∗ 0.054∗∗∗ 0.053∗∗∗(0.011) (0.011) (0.011) (0.011) (0.011) (0.011)Tenure 0.025∗∗∗ 0.025∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.024∗∗∗(0.003) (0.003) (0.003) (0.003) (0.003) (0.003)Leader effect × (Age > threshold) 0.234∗∗ 0.193∗ 0.311∗∗∗ 0.170(0.107) (0.107) (0.102) (0.113)Age > threshold -0.045∗∗∗ -0.038∗∗∗ -0.043∗∗∗ -0.049∗∗∗(0.012) (0.012) (0.012) (0.012)Observations 4249 4249 4249 4249 4249 4249Adjusted R2 0.043 0.044 0.043 0.042 0.044 0.043Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Dependent variable is a promotion dummy. Province and year fixed effects. Standard errors are clustered at the prefecturelevel.44Table 3.2: Reanalysis of Table 4, Yao and Zhang (2015)(1) (2) (3) (4) (5) (6)Threshold: 49 Threshold: 50 Threshold: 51 Threshold: 52Leader effect 0.033 -0.577 -0.030 -0.009 -0.066 -0.012(0.053) (0.657) (0.085) (0.080) (0.072) (0.068)Leader effect × Age 0.012(0.013)Age -0.006∗∗∗ -0.006∗∗∗(0.001) (0.001)Provincial experience 0.051∗∗∗ 0.051∗∗∗ 0.051∗∗∗ 0.052∗∗∗ 0.053∗∗∗ 0.052∗∗∗(0.011) (0.011) (0.011) (0.011) (0.011) (0.011)Tenure 0.025∗∗∗ 0.025∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.024∗∗∗(0.003) (0.003) (0.003) (0.003) (0.003) (0.003)Leader effect × (Age > threshold) 0.111 0.081 0.223∗∗ 0.110(0.114) (0.112) (0.103) (0.111)Age > threshold -0.044∗∗∗ -0.037∗∗∗ -0.042∗∗∗ -0.048∗∗∗(0.012) (0.012) (0.012) (0.012)Observations 4249 4249 4249 4249 4249 4249Adjusted R2 0.043 0.043 0.043 0.042 0.043 0.043Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Dependent variable is a promotion dummy. Province and year fixed effects. Standard errors are clustered at the prefecturelevel.45Figure 3.1: Li et al. (2019), Table 546Table 3.3: Replication of Table 5 in Li et al.(2019): LPM(1) (2) (3) (4)Growth rate (annual) 0.0276 -1.528(0.148) (1.103)Annual growth × target 14.95(10.68)Growth rate (cumulative) 0.0689 -1.343(0.162) (1.063)Cumulative growth × target 13.68(10.20)Observations 6441 6441 6441 6441Adjusted R2 0.157 0.157 0.157 0.157Province-year FE Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Dependent variable is Promotion. Province-year fixed ef-fects. Standard errors clustered at the prefecture level. Covariates:mayor/secretary fixed effect, Age and Age2, Tenure, and Education.Figure 3.2: Promotion rate: prefecture mayorsTable 3.4: Number of times Promotion = 1 by spellSum 0 1 2 3 4 5Frequency 1129 36 16 12 18 5Note: Spell-level data on prefecture mayors from Chen and Kung (2019).47Figure 3.3: Promotion rate: prefecture mayorsTable 3.5: Replication of Table IX, Chen and Kung (2019)Ordered probit LPM Ordered probit LPM(1) (2) (3) (4)GDP Growth 2.698∗∗ 0.379∗∗∗ -0.303 -0.040(1.099) (0.093) (0.689) (0.132)Observations 2549 2549 2549 2549Adjusted R2 0.376 0.008Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Reanalysis of mayor results from Table IX in Chen and Kung (2019).Dependent variable is Promotion. Original promotion variable used inColumns 1-2; my promotion variable used in Columns 3-4. Prefecture andyear fixed effects. Standard errors clustered at the prefecture level. Co-variates: tax revenue growth, log GDP per capita, and log population.48Table 3.6: Provincial leaders, Landry et al. (2018)Secretary Governor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.028 0.026 0.033 0.029 -0.015 -0.024 -0.018 -0.026(0.018) (0.017) (0.027) (0.027) (0.021) (0.023) (0.033) (0.035)Connection 0.013 0.016 0.012 0.016 0.060 0.055 0.060 0.055(0.028) (0.031) (0.029) (0.032) (0.042) (0.048) (0.042) (0.048)GDP × Connection -0.008 -0.005 0.005 0.003(0.034) (0.033) (0.040) (0.041)Observations 249 249 249 249 251 251 251 251Adjusted R2 0.253 0.252 0.250 0.249 0.056 0.060 0.052 0.056Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is the cumulative average of growth (relative to the national average) over a leader’sterm. Baseline controls include log (population), rural population percentage, log (brightness), log (distanceto the higher level government), and the number of competitors at the same level of jurisdiction. Includesyear fixed effects. Politician covariates include quadratics in age and years in office. Standard errors clus-tered at the province level.49Table 3.7: Prefecture leaders, Landry et al. (2018)Secretary Mayor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.004 0.001 0.002 -0.003 0.009 0.011 0.016 0.016(0.007) (0.007) (0.013) (0.013) (0.009) (0.009) (0.019) (0.018)Connection -0.055∗∗∗ 0.001 -0.055∗∗∗ 0.001 -0.093∗∗∗ -0.035∗ -0.093∗∗∗ -0.035∗(0.013) (0.016) (0.013) (0.016) (0.017) (0.020) (0.017) (0.020)GDP × Connection 0.003 0.006 -0.010 -0.007(0.014) (0.014) (0.021) (0.021)Observations 2229 2081 2229 2081 2237 2121 2237 2121Adjusted R2 0.133 0.163 0.133 0.162 0.132 0.161 0.131 0.160Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is the cumulative average of growth (relative to the provincial average) over a leader’sterm. Baseline controls include log (population), rural population percentage, log (brightness), log (distance tothe higher level government), and the number of competitors at the same level of jurisdiction. Includes year,province, and prefecture type fixed effects. Politician covariates include quadratics in age and years in office.Standard errors clustered at the prefecture level.50Table 3.8: County leaders, Landry et al. (2018)Secretary Mayor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.012∗∗∗ 0.008∗ 0.018∗∗∗ 0.009 0.017∗∗∗ 0.012∗∗ 0.030∗∗∗ 0.026∗∗∗(0.004) (0.005) (0.006) (0.007) (0.005) (0.006) (0.007) (0.009)Connection -0.082∗∗∗ -0.002 -0.082∗∗∗ -0.002 -0.087∗∗∗ 0.014 -0.088∗∗∗ 0.014(0.006) (0.009) (0.006) (0.009) (0.007) (0.011) (0.007) (0.011)GDP × Connection -0.012 -0.002 -0.025∗∗∗ -0.025∗∗(0.008) (0.010) (0.010) (0.012)Observations 13266 9838 13266 9838 14644 10084 14644 10084Adjusted R2 0.085 0.133 0.085 0.133 0.089 0.144 0.090 0.144Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is the cumulative average of growth (relative to the prefecture average) over a leader’s term.Baseline controls include log (population), rural population percentage, log (brightness), log (distance to thehigher level government), and the number of competitors at the same level of jurisdiction. Includes year, prefec-ture, and county type fixed effects. Politician covariates include quadratics in age and years in office. Standarderrors clustered at the county level.51Table 3.9: Nonmeritocratic promotion in Tiger provinces?(1) (2) (3)GDP growth -0.098 -0.118 0.314(0.620) (0.648) (0.673)Growth × Tiger province -0.170 -0.225 0.037(1.109) (1.188) (1.257)Age 0.285∗∗ 0.318∗∗(0.130) (0.128)Age squared -0.003∗∗ -0.003∗∗∗(0.001) (0.001)Sex 0.093 0.108(0.094) (0.089)Home prefecture -0.165 -0.170(0.106) (0.107)Connection -0.043 -0.026(0.064) (0.063)Initial GDP 0.058(0.039)Initial Population 0.110∗∗(0.047)Observations 421 418 418Adjusted R2 0.021 0.062 0.094Province FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: spell-level data for mayors with spells starting after2005 and ending before 2013. Tiger province is a dummy vari-able for Shanxi, Jiangxi, and Sichuan. Standard errors clus-tered at the prefecture level.52Table 3.10: Provincial leaders: Jia et al. (2015)Governor Secretary(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12)Jiang era Hu era Jiang era Hu eraGDP growth 0.368 0.827 0.535 0.790 -0.740 -1.904 0.086 -0.241 -0.231 -0.126 -0.431 -0.332(0.667) (0.978) (1.068) (1.531) (1.828) (1.985) (0.894) (0.736) (0.762) (0.546) (0.946) (1.018)Age 0.166 0.183∗ -0.147 -0.189 -0.044 -0.030 0.155 0.217(0.108) (0.091) (0.182) (0.175) (0.118) (0.116) (0.125) (0.149)Age squared -0.001 -0.002∗ 0.001 0.001 0.000 0.000 -0.001 -0.002(0.001) (0.001) (0.002) (0.002) (0.001) (0.001) (0.001) (0.001)Education -0.019 -0.023 0.078 0.108 0.001 -0.006 -0.012 -0.007(0.120) (0.132) (0.141) (0.114) (0.048) (0.041) (0.056) (0.069)Central government experience -0.082 -0.072 -0.021 -0.044 0.139∗∗∗ 0.142∗∗∗ 0.047 0.098∗(0.078) (0.085) (0.116) (0.096) (0.038) (0.036) (0.041) (0.049)Ruling birth province -0.071 -0.073 -0.146 -0.195∗∗ 0.021 0.028 -0.039 -0.047(0.066) (0.076) (0.086) (0.078) (0.058) (0.059) (0.073) (0.062)Growth during previous term -0.641 -1.513 -2.378 -3.116 -0.044 -0.170 -2.677 -3.798(0.899) (0.933) (2.989) (2.887) (1.002) (1.001) (1.988) (2.332)Princeling -0.164∗ -0.460∗∗∗ -0.173∗ -0.122∗(0.081) (0.156) (0.099) (0.066)Workplace connection 0.295∗∗∗ -0.184∗ -0.010 0.020(0.075) (0.090) (0.074) (0.026)Politburo connection 0.065 -0.213∗∗∗ -0.059∗ 0.000(0.092) (0.074) (0.032) (0.046)Observations 266 265 265 212 212 212 273 272 272 215 214 214Adjusted R2 0.011 0.064 0.090 -0.047 0.004 0.074 0.180 0.228 0.223 0.054 0.128 0.127Tenure and spell FEs No Yes Yes No Yes Yes No Yes Yes No Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is cumulative average relative GDP growth (relative to annual mean). Fixed effects for province and year. Standard errors clustered at theprovince level. The Jiang era covers 1993-2002, and the Hu era covers 2003-2009.53Table 3.11: County secretaries: Chen and Kung (2016)LPM Ordered logit(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.086∗∗∗ 0.068∗∗ 0.071∗∗ 0.044 1.168∗∗∗ 1.183∗∗∗ 1.206∗∗∗ 0.415(0.030) (0.032) (0.031) (0.044) (0.309) (0.328) (0.331) (0.484)Growth × Hu era 0.050 1.438∗∗(0.059) (0.648)Age 0.008 -0.001 -0.004 -0.004 0.872∗∗∗ 0.815∗∗∗ 0.794∗∗∗ 0.799∗∗∗(0.014) (0.014) (0.014) (0.014) (0.218) (0.220) (0.219) (0.220)Age squared -0.000 0.000 0.000 0.000 -0.010∗∗∗ -0.010∗∗∗ -0.009∗∗∗ -0.009∗∗∗(0.000) (0.000) (0.000) (0.000) (0.002) (0.002) (0.002) (0.002)Education 0.005∗∗∗ 0.005∗∗∗ 0.004∗∗ 0.004∗∗ 0.071∗∗∗ 0.069∗∗∗ 0.058∗∗∗ 0.058∗∗∗(0.002) (0.002) (0.002) (0.002) (0.019) (0.020) (0.020) (0.020)Initial GDP 0.001 0.001 0.001 0.057 0.053 0.053(0.006) (0.006) (0.006) (0.060) (0.060) (0.059)Initial tax revenue 0.031∗∗∗ 0.029∗∗∗ 0.029∗∗∗ 0.177∗∗∗ 0.160∗∗∗ 0.154∗∗∗(0.006) (0.006) (0.006) (0.055) (0.056) (0.056)Initial population 0.003 0.002 0.002 0.097 0.096 0.101(0.006) (0.006) (0.006) (0.064) (0.065) (0.065)CYL secretary 0.028∗∗∗ 0.028∗∗∗ 0.328∗∗∗ 0.330∗∗∗(0.009) (0.009) (0.099) (0.099)Shared workplace 0.049∗∗∗ 0.049∗∗∗ 0.512∗∗∗ 0.513∗∗∗(0.007) (0.006) (0.071) (0.071)Shared hometown 0.104∗∗∗ 0.104∗∗∗ 0.762∗∗∗ 0.764∗∗∗(0.017) (0.017) (0.113) (0.113)Observations 10208 9653 9653 9653 10609 10105 10105 10105Adjusted R2 0.096 0.099 0.113 0.113Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is cumulative average relative GDP growth. LPM specification includes fixed effects for tenureand Prefecture × Year. Ordered logit specification includes fixed effects for tenure, Prefecture, and Year. Initial Xvariables are calculated during a politician’s first year in office. Standard errors clustered at the prefecture level.54Table 3.12: County leaders: Landry et al. (2018)Secretary Mayor(1) (2) (3) (4) (5) (6)GDP growth 0.012∗∗∗ 0.008∗ 0.003 0.015∗∗∗ 0.008 0.013(0.003) (0.005) (0.007) (0.004) (0.006) (0.008)Growth × Hu era 0.012 -0.011(0.010) (0.012)Connection -0.011 -0.011 -0.003 -0.003(0.014) (0.014) (0.019) (0.019)Age -0.035∗∗ -0.035∗∗ 0.033 0.033(0.016) (0.015) (0.035) (0.035)Age squared 0.000∗∗ 0.000∗∗ -0.000 -0.000(0.000) (0.000) (0.000) (0.000)Tenure 0.065∗∗∗ 0.065∗∗∗ 0.127∗∗∗ 0.127∗∗∗(0.012) (0.012) (0.012) (0.012)Tenure squared -0.003 -0.003 -0.009∗∗∗ -0.009∗∗∗(0.002) (0.002) (0.002) (0.002)Initial population 0.033∗∗∗ 0.033∗∗∗ 0.016∗ 0.016∗(0.007) (0.007) (0.009) (0.009)Observations 14380 9656 9656 15924 9845 9845Adjusted R2 0.154 0.198 0.198 0.178 0.245 0.245Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is cumulative average relative GDP growth. Fixed effects for countytype and Prefecture × Year. Initial population is calculated during a politician’s first yearin office. Standard errors clustered at the prefecture level.55Chapter 4Bunching on the wrong side:Tax enforcement technologyand tax evasionTax administration is different in developing countries. Informal agreements between taxpayersand tax collectors are common (Cui, 2015), bureaucracies have fewer resources, and legal powersoften differ (Robinson and Slemrod, 2012). Such differences are increasingly being recognized asfirst-order determinants of fiscal capacity and tax design, as reflected in the growing interest inadministrative tools to improve compliance in weak-enforcement environments (Brockmeyer andHernandez, 2017; Slemrod et al., 2017; Waseem, 2018). In this paper, we study the role of taxcollector discretion in determining taxpayer compliance.China’s corporate income tax provides preferential rates to small firms through a series ofnotches in the tax schedule.54 Firms with reported taxable income below a given threshold receiveaverage tax rates that are 5 to 15 percentage points lower relative to firms immediately above thethreshold. This strongly incentivizes firms to report income below the threshold. Our motivatingpuzzle is that a significant mass of firms bunch above the notches rather than below. Using datafrom tax returns, we show that bunching-above is explained by tax collectors using an enforcementtechnology, discretion over regulatory procedures, to prevent tax evasion.Tax collectors exercise discretion over a firm’s tax prepayments, which are made quarterlythroughout the year. Specifically, tax collectors decide whether firms prepay at the preferentialrate or the (higher) standard rate. If tax collectors can imperfectly observe whether firms areeligible for the lower rate, they might assign higher prepayment rates to suspected-ineligible firms.This signals to the firm a willingness to audit if the firm reports year-end income below the threshold(and thereby claims the lower tax rate). In response, wanting to avoid a costly audit, these firmsreport income above the threshold, generating the observed bunching-above behavior.To validate this model, we start by showing a strong correlation between prepayments andbunching-above. Firms that prepay at a rate higher than the preferential rate are much more likelyto bunch above the income threshold, consistent with our story of ineligible firms being assigned54A notch is a discrete change in the average tax rate; a kink is a discrete change in the marginal tax rate. Notchesare a common feature of many tax systems (Kleven, 2016).56higher prepayment rates. We then study a policy reform that removed tax collector discretionover prepayments. Following the reform, we observe a sharp drop in firms prepaying more thanthe preferential rate, as well as an increase in bunching-below and a decrease in bunching-above.These findings suggest that, without their enforcement technology, tax collectors were no longerable to prevent ineligible firms from evading taxes by claiming the lower rate. Facing no barriersto evasion, firms claimed the lower rate, generating the expected bunching below the threshold.Thus, we observe the outcomes of a tax enforcement game, where firms try to evade taxes,and tax collectors try to stop them. Unique to our context, tax collectors started out possessingan enforcement technology to prevent evasion, which leads to firms bunching above the threshold.When tax collectors lost this enforcement technology, firms bunch below, as is common in othersettings.While we cannot empirically distinguish evasion from real responses, a substantial body ofliterature supports the notion that firm tax evasion is a first-order response, particularly in low-compliance environments (Best et al., 2015; Waseem, 2018; Bachas and Soto, 2017). Our findingsare broadly complementary to the literature examining tax enforcement mechanisms meant toreduce such evasion (Naritomi, 2016; Kleven et al., 2016; Pomeranz, 2015; Carrillo et al., 2017;Slemrod et al., 2017; Almunia and Lopez-Rodriguez, 2018).55A recurring theme in this literature is that firms respond to enforcement efforts by findingalternative ways to lower their tax bill (Slemrod et al., 2017; Carrillo et al., 2017). We find consistentbehavior in our setting, with firms appearing to strategically adapt their prepayment behavior overtime. Our findings are also complementary to prior research documenting how tax collectors adjustenforcement effort when faced with shocks to revenue streams (Chen, 2017). In our setting, taxcollectors appear to mitigate revenue losses through their discretion over prepayments.The policies we study are among the most prominent used by the Chinese government to encour-age business growth. The preferential 10% rate for small enterprises has evolved from a temporarymeasure to combat the Global Financial Crisis into a general and permanent tax reduction to “al-leviate the burden” on small businesses. The taxable income threshold for the reduced that 10%rate, which started at 30,000 yuan in 2010, was raised to 500,000 in 2017 and then 1,000,000 in2018. Similarly, the regulatory reform introduced in 2014 was also a key development in China’seffort to modernize its tax administration. To our knowledge, this is the first paper to study theeffects of these policies.The remainder of the paper proceeds as follows. Section 4.1 presents an overview of the corporatetax environment, the small business tax preference, and tax prepayment procedures. Section 4.2presents the main cross-sectional patterns of bunching and prepayments. Section 4.3.1 elaborateson the underlying mechanism through which discretion over prepayments generates the observedbunching behavior. Section 4.3.2 exploits the 2014 regulatory reform to study the effect of reduced55Slemrod (2017) and Slemrod and Yitzhaki (2002) offer extensive overviews of the broader literature on enforce-ment and compliance.57tax collector discretion. Section 4.5 concludes.4.1 Institutional details4.1.1 Small business preferential tax ratesFifty-six percent of tax revenue in China came from the VAT and Business Tax56, 21% from thecorporate income tax (CIT), and only 6% from the personal income tax. Within the CIT, firms aretaxed on a standard corporate income tax base. Taxable income is calculated as reported revenueminus reported costs, depreciation, and interest expenses. Dividends are paid out from after-taxincome. The base statutory corporate tax rate was 25% during this period, for both foreign anddomestic firms.Beginning in 2008, “small and micro-profit enterprises” (henceforth SMPEs) could claim apreferential 20% corporate income tax rate. Firms are categorized as small if (i) they are belowan asset and employee threshold57 and (ii) if their taxable income is below 300,000CNY.58 If thesefirms have reported taxable income below an even lower threshold, they are categorized as micro-enterprises and their effective tax rate was reduced further to 10%.59 This lower threshold was30,000 in 2010/11, 60,000 in 2012/13, 100,000 in 2014, 200,000 in 2015, and 300,000 in 2016.Figure 4.1 depicts the statutory rate schedule and evolution of these thresholds.60 While this paperstudies bunching around the thresholds, we focus on the broader effects of tax reductions on firmgrowth and investment in parallel work.4.1.2 PrepaymentsAs in other countries, Chinese firms that are liable for the corporate income tax make prepay-ments throughout the year, and settle their annual income tax liability by the end of May of thenext year. Firms generally prepay on a quarterly basis, while some large firms may be requiredto make monthly advance payments. Firms are expected to prepay according to actual periodicprofit if such profit can be determined. Large taxpayers in principle should follow the actual profitmethod, and prior to 2014, small firms wishing to prepay at the lower preferential tax rate forSMPEs must also prepay on an actual profit basis. For firms that cannot determine actual profit,the prior years quarterly (monthly) average profit is used for making prepayments. Prepayment56A cascading sales tax that was folded into the VAT in between 2012 and 201657The asset thresholds are 30,000,000 CNY and 10,000,000 CNY for industrial and non-industrial firms respectively,and the employee thresholds 100 and 80 respectively.58The purchasing power parity exchange rate during this period was around 3.5, therefore in comparable USD, thisis around $86,000. At a 4 percent profit rate, this implies annual sales of around 7.5 million (CNY) or 2.15 million(USD).59This is achieved through allowing taxpayers to include only half of their taxable income in the computation oftax liability.60In June 2017, it was announced that for 2017-2019, the taxable income threshold for the reduced 10% rate wouldbe raised to 500,000 yuan, and in 2018 it was further increased to 1 million yuan.58methods are also subject to discussion with the tax authority: if prepayment falls far short ofultimate tax liability in a given year, the tax authority may require another prepayment methodof the taxpayer going forward.Tax agencies face agency internal targets for aggregate levels of prepayment, generally set inrecent years at 70% of ultimate tax payable. Such targets seem easily met by the firms we observe.Appendix Figure C.2 shows the distribution of the share of final tax liability that was paid inadvance. Most firms prepay between 70 and 100%.Prior to 2014, in order to make prepayments according to the preferential tax rates, small en-terprises had to demonstrate their eligibility when filing quarterly (monthly) returns accompanyingtheir periodic prepayments. Tax authorities were authorized, if they deem the evidence of eligibilityinsufficient, to deny taxpayers the option of prepaying at the preferential rate. In April 2014, as apart of a national effort to reduce government regulation, this procedure for verifying SMPE eligi-bility for reduced prepayment was eliminated. In addition, as the national government increasinglyrelied on the 10% reduced rate for SMPEs as a policy instrument, by 2016 tax bureaus began touse the thorough implementation of the preferential policy as a performance metric for evaluatingtax collectors. All of these factors – in addition to small taxpayers and tax collectors learning moreabout the policy and its implementation – may contribute to greater ease over time in obtainingthe preferential treatment.4.1.3 Offsets and refundsAfter the closing of a tax period61, if a firm determines that its income tax liability is lower thanthe amount prepaid, it may apply either for a refund or for an offset against current year liabilities.Typically, a refund is issued (instead of an offset) only if the amount of the over-payment is large.The application is nominally simple and requires the taxpayer to submit relatively few items ofdocumentation and only simple explanations. However, tax agencies can offset any over-paymentfor the income tax against any other outstanding tax liability of the taxpayer before issuing arefund.4.2 Bunching-above and prepaymentsWe document three main facts: that firms bunch below and above the notches, and thatbunching-above is strongly predicted by prepayments.4.2.1 Substantial bunching occurs below the thresholdFigure 4.2 plots the distribution of reported taxable income for the micro-enterprise thresholds.As a placebo test, we plot the distribution for adjacent years in which the threshold was not present.61The end of a calendar year or the closing of the firm in the midst of a calendar year.59Consistent with predictions, firms bunch below the thresholds. Firms may do so through evasion,avoidance, or reducing real activity. When the threshold moves, bunching disappears. Figure 4.3demonstrates the same phenomenon around the small enterprise threshold (300,000 CNY). Sincethis threshold was constant throughout our sample, we use the distribution of ineligible firms as aplacebo.62 Ineligible firms do not bunch, while eligible firms do.4.2.2 Substantial bunching occurs above the thresholdApparent in both Figures 4.2 and 4.3 is the substantial bunching above of the notch. Indeed,for the years 2010-2014, the number of firms bunching above the threshold is equal to or largerthan the number bunching-below. Considering the magnitude of the tax reduction around thethresholds, it is implausible that such a large mass of firms accidentally report taxable incomeas (say) 301,000 rather than 300,000. Similarly, the large mass cannot be explained by fixed orvariable costs of adjusting taxable income – this would imply that the counter-factual distributionalso contains bunching above the notch, which is ruled-out by the placebo distributions. We willargue that bunching-above is driven by strategic interactions between firms and tax collectors.4.2.3 Bunching-above is strongly predicted by prepaymentsThe notches in the tax schedule create two implicit prepayment benchmarks. Consider a firmwith taxable income around 30,000. If the firm reports taxable income of exactly 30,000, their taxbill in 2010 would be 3000 at the preferential 10% rate. If they report taxable income of 30,001– thereby disqualifying them from the 10% rate – the resulting tax liability would be 6000. Wedefine the lower prepayment threshold as the amount a firm would prepay if (i) its taxable incomeexactly equals the threshold and (ii) prepayment was made at the preferential tax rate (3000 in theexample above). We define the upper prepayment threshold as the tax liability at the higher rate(6000 in the example above). These thresholds have no inherent legal meaning. The two thresholdsgenerate three implicit prepayment regions: below the lower threshold, between the lower and upperthreshold, and greater than the upper threshold.According to tax law, the amount of prepayment should have no bearing on year-end taxableincome: a firm is obliged to report taxable income, receive a refund or offset for excess prepayments,or make additional payments if prepayments are lower than the amount due. Nonetheless, wedocument a striking relationship between the prepayment thresholds and reported tax liability.Indeed, the lack of legal significance makes the following patterns all the more intriguing.To start, Figure 4.4 presents taxable income bunching patterns for firms in each prepaymentregion. For each group of firms, we plot the distribution of reported income around the notches.62We determine eligibility based on reported balance sheet assets. This measure of eligibility is imperfect as itomits the employee count criteria, and because the total asset measure we observe is not necessarily the same as thatused by tax collectors for determining eligibility.60Firms in the lowest prepayment region are most likely to bunch-below, while firms in the highestprepayment region are least likely to bunch at all. Firms in the middle region, between the twohypothetical tax liabilities, are dramatically more likely to bunch just above the notch. AppendixFigure C.3 shows the same result when plotting prepayment patterns by firms bunching above vs.below.Next, we show in Figure 4.5 that this pattern corresponds to a sharp discontinuity in the prob-ability of bunching-above. In this graph, we restrict the sample to firms in a narrow bandwidtharound the taxable income threshold (“bunchers”). Among these bunchers, we plot the correlationbetween prepayment and the probability of bunching-above rather than below.63 There is a sub-stantial discontinuity in the probability of bunching-above around the lower prepayment threshold.Panel A shows that moving from 2900 to 3100 in prepayments is associated with a roughly 40percentage-point increase in the probability of bunching-above. Panels B and C show the samepattern in 2012/13 and 2014.We conclude that there is a strong correlation between firms bunching-above and having prepaidmore than their final tax liability conditional on claiming the lower tax rate.64 As we discuss inthe next section, we interpret this correlation as tax collectors assigning high prepayment ratesto suspected-ineligible firms, who in response report taxable income just above the threshold,generating the observed bunching-above.4.2.4 Additional resultsIn Appendix Section C.1, we find evidence that some firms persistently bunch above or belowthe threshold in consecutive years. Appendix Section C.2 shows that larger firms are somewhatmore likely to bunch above the threshold.4.3 Model and evidence4.3.1 MechanismIn this section, we propose a mechanism that rationalizes the empirical patterns, based on theassumption that tax collectors have both the information and enforcement technology to preventtax evasion. Then, in Section 4.3.2, we provide supporting evidence from a policy change thatremoved tax collectors’ enforcement technology.Firms can evade taxes by manipulating their taxable income to be below the threshold and63Specifically, we group these firms into equal-width prepayment bins, and for each bin, we plot the percentage offirms within that bin that are above the threshold versus just below.64That is, if a firm prepaid between 3000 and 6000 in 2010/2011, and also reported income below the 30000threshold, then their prepayments would exceed their liability (which would be less than 3000).61thereby claiming the preferential 10% rate.65 To deter evasion, tax collectors use their enforcementtechnology, discretion over prepayment rates, to assign higher prepayment rates to suspected taxevaders. We assume that tax collectors can imperfectly observe eligibility for the preferential rate.This assumption is plausible because tax collectors manage a pool of firms, and interact with themfrequently and in person, allowing the tax collectors to acquire first-hand knowledge of a firm’sincome.Assigning a higher prepayment rate signals a willingness of the tax collector to audit the firmif it reports income below the threshold.66 Facing the threat of a costly audit, the firm’s bestresponse is to avoid additional scrutiny by reporting their taxable income above the threshold,while also minimizing their tax liability. That is, firms bunch immediately above the threshold.This mechanism generates the observed bunching-above behavior, as well as the correlation betweenprepayments and bunching-above observed in Figure 4.5.To validate this model, we provide evidence from a policy change that removed tax collec-tors’ enforcement technology by eliminating tax collector discretion over prepayments. This policychange shuts down the signalling mechanism described above. If tax collectors cannot assign higherprepayment rates to suspected-ineligible firms, then there is no audit threat, and hence no reasonfor firms to bunch-above. Without discretion over prepayments, there should be no correlationbetween prepayments and the probability of bunching-above. Hence, our model makes three pre-dictions. First, a decrease in bunching-above the notches, as firms no longer face a cost to claimingthe lower rate. Second, a decrease in the number of firms in the middle prepayment region, as taxcollectors cannot assign higher prepayment rates.67 And third, a decrease in the discontinuity inthe probability of bunching-above at the lower prepayment threshold, as suspected evaders are nolonger assigned higher prepayment rates (with the attendant audit threat), and so, conditional onprepaying a higher rate, it is no longer a best-response to bunch-above. We explore these predictionsin the next section.4.3.2 Evidence from a policy reformIn July 2014, as a part of a national effort to reduce government regulation, the governmentchanged several tax administration procedures related to the small- and micro-enterprise preferen-tial tax rates.68 One of the broad motivations for this reform was to increase the number of firmspaying at the lower tax rates. The policy instructions imply that local tax bureaus did in fact issue65Given the magnitude of the notch (a 10pp reduction in the average tax rate), it would be profit-maximizing forsome firms to increase real costs as a way of reducing taxable income.66Formal audits are rare. However, firms interact frequently with tax collectors, so tax collectors can impose costson firms through increased scrutiny. We use “audit broadly to mean costly tax collector scrutiny.67Note that it is suboptimal for firms to prepay in the middle region, in terms of tax planning. They must either(1) submit another payment, if their income exceeds the threshold and they pay the higher rate; or (2) request arefund (or accept a loss), if their income is below the threshold and they pay the lower rate.68We present the relevant text from the policy directive in Appendix Section C.3.62their own approval requirements, consistent with our model of tax collectors exercising discretionover prepayments.69In particular, this reform removed approval processes for firms prepaying at the preferentialrates. Firms were now allowed to determine their own eligibility for prepaying at the lower rate.In other words, tax collectors effectively lost their discretion over prepayments, and on our model,lost their enforcement technology for preventing evasion. After the reform, tax collectors were nolonger able to assign higher prepayment rates to suspected-ineligible firms, as a means of signallingan audit threat to tax evaders.Next we evaluate the three predictions from our model. First, Figure 4.6 shows that bunching-above decreased after the reform. As with previous figures, we restrict the sample to bunchers,and plot for each year the probability of bunching-above. In the year prior to the reform, roughly50 percent of bunchers were above the threshold. Two years after the reform, it dropped to 30percent. Consistent with our model, once the signalling mechanism is shut down, firms no longerhave a reason to report income above the threshold. However, bunching-above decreases graduallyover the post-reform years, and does not disappear entirely by 2016. It is possible that the policyreform was not implemented immediately, and that it took several years for tax collector discretionto be removed at the ground level. We also remain open to the possibility that other factors areplaying a role.Second, Figure 4.7 shows a stark decrease in the proportion of firms prepaying in the middleprepayment region. The proportion falls from 35% to 15% immediately after the reform, for boththresholds.70 This behavior is consistent with tax collectors losing the ability to assign higherprepayment rates to suspected-ineligible firms. As noted above, prepaying in the middle region issuboptimal, so firms would avoid doing so unless some other factor was influencing their decisions.In our model, this factor is tax collector discretion over prepayments, which was removed by thereform.Third, we test whether the correlation between prepayments and bunching-above changed afterthe reform. In particular, we expect the discontinuity in the probability of bunching-above inFigure 4.5 to shrink after 2014. Formally, for a given taxable income notch Tt, we calculatethe implicit lower prepayment threshold Tp = τlower × Tt in year t, then estimate the changein the probability of bunching-above, ∆, as prepayment crosses Tp.71 The running variable is69The policy also instructed tax collectors to improve access to refunds, implying that refunds were too costly forfirms to obtain.70We also observe bunching at the implicit prepayment thresholds, as shown in Appendix Figures C.4–C.5. Thisis explained by bunching at the income threshold, combined with the assumption that firms tend to prepay 100% oftheir tax liability. In particular, firms bunching below the income threshold will bunch below the lower prepaymentthreshold, and firms bunching above the income threshold will bunch above the upper prepayment threshold. Sincethere is still some bunching-above the income threshold in 2016, we also see bunching above the upper prepaymentthreshold. For example, a firm reporting income of 301000 in 2016 will owe 0.25 × 301000 = 75250; if they prepaythis amount, they will be just above the upper prepayment threshold.71We implement the bias-corrected RD estimator and standard errors developed by Calonico et al. (2014), andimplemented in Stata by Calonico et al. (2017), with the MSE-optimal bandwidth introduced by Imbens and Kalya-63prepayment, and the discontinuity is estimated at Tp. Thus, the RD model is 1{bunch-above}it =α + βDit + f(t) + g(t)Dit + εit, where Dit is an indicator for being above the lower prepaymentthreshold, and f and g are quadratic polynomials of prepayments. Figure 4.8 plots the estimatesof ∆ for both thresholds, for each year from 2010 to 2016. For the micro-enterprise threshold, thediscontinuity drops to zero immediately after the reform. We do not see a similar pattern for thesmall-enterprise threshold.Overall, we conclude that our proposed mechanism is playing at least some role in the observedbunching-above behavior. As bunching-above does not disappear after the reform, we acknowledgethat our mechanism does not fully explain the data. However, as we show in the next section,alternative explanations are not able to rationalize the observed patterns.4.4 Alternative explanations for bunching-aboveAn alternative explanation for bunching-above is based on the premise that tax collectors areaverse to granting refunds, either to avoid losing tax revenue, or simply to avoid paperwork. Asnoted above, firms with excess prepayments would be eligible for a refund if they reported incomebelow the threshold. If tax collectors are reluctant to offer refunds, they may persuade or coercerefund-eligible firms (those in the middle prepayment region) to report taxable income above thethreshold, where they are no longer eligible for a refund. This mechanism generates bunching-above, as well as the correlation between excess prepayments and bunching-above seen in Figure4.5.This explanation is plausible, because the policy directive instructed tax collectors to makerefunds more accessible to firms, implying that tax collectors were somewhat averse to grantingrefunds prior to the reform. This leads to the testable implication that there was a level increasein number of refunds granted after the reform. However, as shown in Appendix Figure C.6, we donot observe a level increase in the number of refunds. While there is a stunning spike in refundsin September 2014, this is not consistent with the policy reform generically reducing the cost ofobtaining a refund. Hence, this prediction of the refund-aversion model is not confirmed.Furthermore, this mechanism does not explain why firms prepay in the middle region in thefirst place. Middle prepayment is puzzling, because it is suboptimal for the firm. If a middleprepayment firm reports year-end income above the threshold, then they pay at the higher rate,and since their prepayments are less than their liability, they must make another payment. If thefirm reports income below the threshold, then they pay at the lower rate and their prepaymentsare greater than their liability; in this case, they can request a refund or else lose the overpaidtaxes. Hence, to avoid extra paperwork, the firm will optimally prepay outside of the middleregion. But the refund-aversion story simply takes the existence of middle-prepayers as given,naraman (2012).64when in fact it requires explanation.72 Under the signalling mechanism, this behavior is explainedas tax collectors using their discretion to require firms to prepay in the middle region. When thisdiscretion is removed by the policy reform, middle prepayment falls sharply, as shown in Figure4.7. Hence, the refund aversion model does not explain the data.An explanation that is complementary to our signalling model is that the policy directiveexplicitly targeted the number of firms claiming the preferential rate. Specifically, the policy reformmade access to the lower rates into a formal performance metric for tax bureaus.73 Hence, we shouldexpect an increase in firms claiming the lower rate (and bunching below the threshold) as an effectof the reform. While not providing a specific explanation for the decrease in bunching-above, to theextent that there are other reasons (besides our signalling model) why firms were bunching abovethe threshold, this effect of the policy reform would help explain a decrease in bunching-above andan increase in bunching-below.4.5 ConclusionConsistent with the literature on tax enforcement, we document substantial bunching aroundnotches in China’s corporate income tax schedule. Unlike previous studies, however, we find asubstantial mass of firms bunching above these notches. Our explanation for this puzzling behavioris that tax collectors use discretion over prepayments as an enforcement technology to preventevasion. Tax collectors assign higher prepayment rates to ineligible firms, which signals to the firma willingness to audit if the firm claims the lower tax rate (by reporting income below the threshold).In response, wanting to avoid a costly audit, firms bunch above the threshold. We validate thisexplanation by using a policy reform that removed tax collectors’ discretion over prepayments.Following the reform, bunching-above decreased and bunching-below increased, consistent with amodel where firms were initially blocked from evading. When tax collectors lost their enforcementtechnology, they were no longer able to prevent evasion.Studies of tax evasion commonly find bunching below notches. This is the natural predictionwhen we expect tax collectors to have no enforcement technology for preventing evasion. Our settingis unique, as local Chinese tax collectors did in fact have an imperfect enforcement technology:discretion over prepayments. The puzzle of bunching-above is explained by tax collectors preventingevasion.72One independent explanation is that firms learn over time that prepaying in the middle region is suboptimal.But this does not explain the sharp drop in middle prepayment following the reform.73In the province we study, implementation of various tax policy measures targeted at small businesses was given25 points (out of 1,000) in 2016 internal performance metrics, with points deducted if implementation is less than100%. In 2017, implementing the income tax policy for SMPEs was given 15 points (out of a total 900 points) inperformance measurement, with all points forfeited if implementation was less than 97%.654.6 Tables and figuresFigure 4.1: Evolution of the corporate income tax schedule for eligible firms0 50 100 150 200 250 300 35010152025Reported taxable income (1000s)Averagetaxrate2010-2011 2012-2013 20142015 2016Note: This figure depicts the evolution of the corporate income tax schedule from 2010 to 2016 for firms with assetsand employees below the eligibility cutoffs. If reported taxable income is greater than 300,000 CNY, the averagetax rate is 25 percent. If reported taxable income is less than or equal 300,000, the small enterprise threshold, buthigher than the micro enterprise threshold, the average tax rate is 20 percent. If reported taxable income is belowthe micro enterprise threshold, which has increased over time, then the average tax rate is 10 percent. In 2015, thetax authority announced that the micro-enterprie threshold would be increased from 200,000 to 300,000, effectivelycombining the small and micro thresholds. Taxable income corresponding to the last quarter of 2015 was eligible toreceive the preferential rate of 10 percent. Thereby, a firm with final taxable income between 200,000 and 300,000would pay face a 17.5 percent tax rate, rather than 20 percent. The PPP exchange rate with USD was roughly 3.5during this period, making a 300,000 threshold equivalent to roughly 86,000 USD.66Figure 4.2: Bunching at the micro-enterprise thresholds(a) 2010-2011.01.02.03.04.05.06Frequency10000 20000 30000 40000 50000Taxable Income2010-2011 2012-2013(b) 2012-2013.02.04.06.08.1Frequency40000 50000 60000 70000 80000Taxable Income2012-2013 2014(c) 2014.01.02.03.04.05.06Frequency70000 80000 90000 100000 110000 120000 130000Taxable Income2014 2013(d) 2015.02.04.06.08Frequency140000 160000 180000 200000 220000 240000 260000Taxable Income2015 2014Note: This figure plots the distribution of firms around the taxable income thresholds depicted in Figure 4.1. The markers represent the right-handendpoint of a taxable income bin (inclusive). The panels plot the distribution during the year(s) which the threshold was in place, and contrasts this toadjacent the distribution in years during which the threshold was absent. For instance, Panel A plots the distribution in 2010/11 and 2012/13 aroundthe lower threshold which was 30,000 in 2010/11. In 2012/13, the threshold increased to 60,000. Multi-year distributions, such as 2010/11 and 2012/13,represent firm-years, rather than the number of firms. Source: Authors’ calculations.67Figure 4.3: Bunching at the small-enterprise threshold0.01.02.03.04Frequency100000 200000 300000 400000 500000Taxable Income20130.01.02.03.04Frequency100000 200000 300000 400000 500000Taxable Income20140.02.04.06Frequency100000 200000 300000 400000 500000Taxable Income20150.01.02.03.04Frequency100000 200000 300000 400000 500000Taxable Income2016Eligible IneligibleNote: This figure plots the distribution of firms around the small enterprise notches depicted in Figure 4.1. The markers represent the right-hand endpointof a taxable income bin (inclusive). For a given year, the panels plot the distribution of eligible firms and the distribution of ineligible firms as a placebo.A firm is eligible if their employee count and asset value are both lower than the qualifying thresholds. In practice, we do not observe employee counts,and therefore classify firms as eligible based soley on the asset threshold. Source: Authors’ calculations.68Figure 4.4: Bunching by prepayment grouping(a) 2010-2011 Micro Enterprise0.05.1Frequency15000 20000 25000 30000 35000 40000 45000Taxable IncomePrepayment < 3000 Prepayment >6000 3000< Prepayment <6000(b) 2012-2013 Micro Enterprise0.05.1.15.2Frequency40000 45000 50000 55000 60000 65000 70000 75000 80000Taxable IncomePrepayment < 6000 Prepayment >12000 6000< Prepayment <12000(c) 2014 Micro Enterprise0.05.1.15Frequency80000 85000 90000 95000 100000 105000 110000 115000 120000Taxable IncomePrepayment < 10000 Prepayment >20000 10000< Prepayment <20000(d) 2015 Micro Enterprise0.05.1.15.2Frequency170000 180000 190000 200000 210000 220000 230000Taxable IncomePrepayment < 20000 Prepayment >35000 20000< Prepayment <35000 (e) Pre-2016 Small Enterprise0.05.1.15Frequency250000 260000 270000 280000 290000 300000 310000 320000 330000 340000 350000Taxable IncomePrepayment <= 60000 Prepayment >75000 30000< Prepayment <75000 (f) 2016 Small Enterprise0.05.1.15Frequency250000 260000 270000 280000 290000 300000 310000 320000 330000 340000 350000Taxable IncomePrepayment <= 30000 Prepayment >75000 30000< Prepayment <75000Note: Firms are separated into groups according to the amount of taxes they prepaid: (1) less than or equal the taxliability at the preferential rate with taxable income exactly equal the notch point, (2) more than the tax liability atthe standard rate with taxable income exactly equal the notch point, and (3) between (1) and (2). Conditional onbeing in one of three pre-payment bins, the densities plots the frequency of firms in each taxable income bin. Multi-year distributions, such as 2010/11 and 2012/13, represent firm-years, rather than the number of firms. Source:Authors’ calculations.69Figure 4.5: Tax prepayments and bunching-above, micro enterprise thresholds(a) 2010-2011 Micro Threshold0.2.4.6.81Percent Wrong-Side Bunching0 1000 2000 3000 4000 5000 6000 7000 8000Prepayments(b) 2012-2013 Micro Threshold0.2.4.6.81Percent Wrong-Side Bunching0 2000 4000 6000 8000 10000 12000 14000 16000Prepayments(c) 2014 Micro Threshold0.2.4.6.81Percent Wrong-Side Bunching6000 8000 10000 12000 14000 16000 18000 20000 22000 24000 26000Prepayments(d) 2012-2013 Small Threshold0.2.4.6.81Percent Wrong-Side Bunching40000 45000 50000 55000 60000 65000 70000 75000 80000 85000 90000Prepayments(e) 2014 Small Threshold0.2.4.6.81Percent Wrong-Side Bunching40000 45000 50000 55000 60000 65000 70000 75000 80000 85000 90000PrepaymentsNote: This figure restricts the sample to firms with taxable income within 5 percent of the threshold on eitherside. We then group firms into equal-width bins based on the amount of taxes prepaid. For each bin, we plot thepercent of firms above the taxable income notch. Large circles imply larger cell sizes. The vertical red lines indicatethe hypothetical tax bill at the preferential and standard tax rates if reported taxable income is exactly equal thethreshold amount (60,000 ×.1 and 60,000 ×.2 in 2012/2013). Source: Authors’ calculations.70Figure 4.6: Ratio of bunching-above to bunching-below.2.3.4.5.6.7Proportion2010 2011 2012 2013 2014 2015 2016Micro-enterprise threshold Small-enterprise thresholdNote: In this figure we plot the percent of bunchers that bunch above the threshold. For a given taxable incomenotch, we restrict the sample to firms with taxable income within a 5 percent window around the notch – these firmsare the “bunchers”. We then calculate the percent of bunchers below and above the notch. 95% confidence intervalsare reported.71Figure 4.7: Decrease in proportion of bunchers in middle prepayment region.1.2.3.4.5Proportion2010 2011 2012 2013 2014 2015 2016Micro-enterprise threshold Small-enterprise thresholdNote: this figure plots the percent of bunchers prepaying in the middle prepayment region. For a given taxableincome notch, we restrict the sample to firms with taxable income within a 5 percent window around the notch –these firms are the “bunchers”. We then calculate the percent of bunchers making prepayments between the implicitprepayment thresholds. 95% confidence intervals are reported.72Figure 4.8: Regression discontinuity estimate of P(bunching-above) at lower prepayment threshold-.20.2.4.6.811.2RD Point Estimate2010 2011 2012 2013 2014 2015 2016YearMicro Enterprise Threshold Small-Enterprise ThresholdNote: We first use regression discontinuity to estimate the jump in the probability of wrong-side bunching at theimplicit lower prepayment threshold for each year. This jump in probability is visualized in Figure 4.5. We plot thediscontinuity estimate for each year along with the its 95 percent confidence interval.73Chapter 5ConclusionThis thesis studied two political economy questions in the context of modern China. First, inChapter 2 I explored a prominent explanation for China’s economic rise: meritocratic promotion.If mayors are selected for political advancement based on their record in growing the economy, thenthey are strongly incentivized to boost GDP growth. Hence, China’s rapid growth can be explainedby its system of meritocratic promotion. However, studying prefecture mayors, I found no evidenceof a correlation between growth and promotion. Using 20 years of data, multiple definitions ofpromotion, various measures of GDP growth, and several regression models, I could not find anyevidence that mayors with higher GDP growth were more likely to be promoted. Contrary to theliterature, I found a null result. This null result cannot be explained away by other factors. I foundno heterogeneous effects over time or by region. I showed that meritocratic promotion is not beingimplemented only for politically connected mayors, or for mayors that are environmentally friendly.And I showed that my null result could not be explained by the 2012 corruption crackdown.In Chapter 3, I confronted the tension between my null result and the published work findingevidence for meritocracy, by reanalyzing five papers from the literature. Using the original data,but making reasonable specification changes, I re-estimated the correlation between promotion andGDP growth. In each case, I found that the original results were not robust. I concluded thatthe tension between my Chapter 2 result and the literature was dissolved, because the evidence inthe literature was not robust. Hence, returning to the original goal of explaining Chinese economicgrowth, I concluded that meritocratic promotion of prefecture leaders was not a valid explanation.However, I did find evidence for meritocratic promotion of county leaders. Since county leaders aredirectly incentivized to boost growth, and since prefecture leaders are selected based on their growthperformance as county leaders, I concluded that meritocracy can still be a genuine explanation forChina’s growth, but in a more sophisticated model than originally proposed.Chapter 4 investigated a different topic: tax evasion by Chinese corporations. My co-authorsand I found a puzzling behavior, with firms seemingly choosing to pay a higher tax rate, when thetax rate jumped discontinuously. That is, we found bunching, as expected, but unexpectedly, itwas on the wrong side of the threshold. We explained this puzzle by constructing a model wheretax collectors use an enforcement technology, discretion over prepayments, to prevent firms fromevading. Tax collectors assign higher prepayment rates to suspected tax evaders, as a signal todeter evasion. In response, firms do not evade, and bunch above the notch. To substantiate thisinterpretation, we studied a policy reform that removed tax collector discretion over prepayments.74Following the reform, bunching above the notches decreased substantially. Without their enforce-ment technology, tax collectors were no longer able to prevent evasion. We concluded that ourpuzzle was explained by Chinese tax collectors being unique in having, at least for a time, theability to prevent tax evasion.75BibliographyAlmunia, Miguel and David Lopez-Rodriguez, “Under the radar: The effects of monitoringfirms on tax compliance,” American Economic Journal: Economic Policy, 2018, 10 (1), 1–38.Aronow, Peter M. and Cyrus Samii, “Does Regression Produce Representative Estimates ofCausal Effects?,” American Journal of Political Science, 2016, 60 (1), 250–267.Bachas, Pierre and Mauricio Soto, “Not(ch) Your Average Tax System: Corporate TaxationUnder Weak Enforcement,” Working Paper, 2017, (April), 1–56.Bai, Chong-En, Chang-Tai Hsieh, and Zheng Song, “Special Deals with Chinese Character-istics,” NBER Macroeconomics Annual 2019, volume 34, 2019, pp. 341–379.Best, Michael Carlos, Anne Brockmeyer, Henrik Jacobsen Kleven, Johannes Spin-newijn, and Mazhar Waseem, “Production versus Revenue Efficiency with Limited TaxCapacity: Theory and Evidence from Pakistan,” Journal of Political Economy, 2015, 123 (6),1311–1355.Brandt, Loren, Debin Ma, and Thomas G. Rawski, “From Divergence to Convergence:Reevaluating the History behind China’s Economic Boom,” Journal of Economic Literature,March 2014, 52 (1), 45–123.Brockmeyer, Anne and Marco Hernandez, “Taxation, Information and Witholding: EvidenceFrom Costa Rica,” 2017.Calonico, Sebastian, Matias D. Cattaneo, and Rocio Titiunik, “Robust NonparametricConfidence Intervals for Regression-Discontinuity Designs,” Econometrica, 2014, 82 (6), 2295–2326., , Max H. Farrell, and Roc´ıo Titiunik, “Rdrobust: Software for regression-discontinuitydesigns,” Stata Journal, 2017, 17 (2), 372–404.Carrillo, Paul, Dina Pomeranz, and Monica Singhal, “Dodging the Taxman: Firm Mis-reporting and Limits to Tax Enforcement,” American Economic Journal: Applied Economics,2017, 9 (2), 144–164.76Chen, Shawn Xiaoguang, “The effect of a fiscal squeeze on tax enforcement: Evidence from anatural experiment in China,” Journal of Public Economics, 2017, 147, 62–76.Chen, Shuo, Xinyu Fan, and Zhitao Zhu, “The Promotion Club,” working paper, 2019.Chen, Ting and James K.-S. Kung, “Do land revenue windfalls create a political resourcecurse? Evidence from China,” Journal of Development Economics, 2016, 123, 86 – 106.and , “Busting the Princelings: The Campaign Against Corruption in China’s Primary LandMarket,” The Quarterly Journal of Economics, 2019, 134 (1), 185–226.Chen, Ye, Hongbin Li, and Li-An Zhou, “Relative performance evaluation and the turnoverof provincial leaders in China,” Economics Letters, 2005, 88 (3), 421 – 425.Clemens, Michael A., “The Meaning of Failed Replications: A Review and Proposal,” Journalof Economic Surveys, 2017, 31 (1), 326–342.Cui, Wei, “Administrative decentralization and tax compliance: A transactional cost perspective,”University of Toronto Law Journal, 2015, 65 (3), 186–238.Fisman, Raymond, Jing Shi, Yongxiang Wang, and Weixing Wu, “Social Ties and theSelection of China’s Political Elite,” American Economic Review, 2020, 110 (6), 1752–81.Francois, Patrick, Francesco Trebbi, and Kairong Xiao, “Factions in Nondemocracies: The-ory and Evidence from the Chinese Communist Party,” working paper, 2020.Gelbach, Jonah B., “When Do Covariates Matter? And Which Ones, and How Much?,” Journalof Labor Economics, 2016, 34 (2), 509–543.Imbens, Guido and Karthik Kalyanaraman, “Optimal bandwidth choice for the regressiondiscontinuity estimator,” Review of Economic Studies, 2012, 79 (3), 933–959.Jia, Ruixue, “Pollution for Promotion,” Working paper, 2017., Masayuki Kudamatsu, and David Seim, “Political Selection in China: The Complemen-tary Roles of Connections and Performance,” Journal of the European Economic Association,2015, 13 (4), 631–668.Jiang, Junyan, “Making Bureaucracy Work: Patronage Networks, Performance Incentives, andEconomic Development in China,” American Journal of Political Science, 2018, 62 (4), 982–999.Kleven, Henrik Jacobsen, “Bunching,” Annual Review of Economics, 2016, 8 (1), 435–464., Claus Thustrup Kreiner, and Emmanuel Saez, “Why Can Modern Governments TaxSo Much? An Agency Model of Firms as Fiscal Intermediaries,” Economica, 2016, 83 (330),219–246.77Landry, Pierre F., Xiaobo Lu, and Haiyan Duan, “Does Performance Matter? EvaluatingPolitical Selection Along the Chinese Administrative Ladder,” Comparative Political Studies,2018, 51 (8), 1074–1105.Li, Hongbin and Li-An Zhou, “Political turnover and economic performance: the incentive roleof personnel control in China,” Journal of Public Economics, 2005, 89 (9), 1743 – 1762.Li, Xing, Chong Liu, Xi Weng, and Li-An Zhou, “Target Setting in Tournaments: Theoryand Evidence from China,” The Economic Journal, 2019, 129 (623), 2888–2915.Lorentzen, Peter and Xi Lu, “Personal Ties, Meritocracy, and Chinas Anti-Corruption Cam-paign,” Working paper, 2018.Lyu, Changjiang, Kemin Wang, Frank Zhang, and Xin Zhang, “GDP management tomeet or beat growth targets,” Journal of Accounting and Economics, 2018, 66 (1), 318 – 338.Naritomi, Joana, “Consumers as Tax Auditors,” Working paper, 2016.Persson, Petra and Ekaterina Zhuravskaya, “The Limits Of Career Concerns In Federalism:Evidence From China,” Journal of the European Economic Association, 2016, 14 (2), 338–374.Pomeranz, Dina, “No taxation without information: Deterrence and self-enforcement in the valueadded tax,” American Economic Review, 2015, 105 (8), 2539–2569.Robinson, Leslie and Joel Slemrod, “Understanding multidimensional tax systems,” Interna-tional Tax and Public Finance, 2012, 19 (July 2011), 237–267.Serrato, Juan Carlos Suarez, Xiao Yu Wang, and Shuang Zhang, “The limits of meritoc-racy: Screening bureaucrats under imperfect verifiability,” Journal of Development Economics,2019, 140, 223 – 241.Sheng, Yumin, “Performance-based Authoritarianism Revisited: GDP Growth and the PoliticalFortunes of China’s Provincial Leaders,” Modern China, (forthcoming).Shih, Victor, Christopher Adolph, and Mingxing Liu, “Getting Ahead in the Commu-nist Party: Explaining the Advancement of Central Committee Members in China,” AmericanPolitical Science Review, 2012, 106 (1), 166187.Slemrod, Joel, “Tax Compliance and Enforcement,” Working Paper, 2017, pp. 1–95.and Shlomo Yitzhaki, Tax avoidance, evasion, and administration, Vol. 3, Elsevier MassonSAS, 2002.78, Brett Collins, Jeffrey L. Hoopes, Daniel Reck, and Michael Sebastiani, “Does credit-card information reporting improve small-business tax compliance?,” Journal of Public Eco-nomics, 2017, 149, 1–19.Su, Fubing, Ran Tao, Lu Xi, and Ming Li, “Local Officials’ Incentives and China’s EconomicGrowth: Tournament Thesis Reexamined and Alternative Explanatory Framework,” China &World Economy, 2012, 20 (4), 1–18.Wang, Bin and Yu Zheng, “A Model of Tournament Incentives With Corruption,” Journal ofComparative Economics, 2020, 48 (1), 182 – 197.Wang, Shaoda, “Fiscal Competition and Coordination: Evidence from China,” Working paper,2016.Waseem, Mazhar, “Taxes, informality and income shifting: Evidence from a recent Pakistanitax reform,” Journal of Public Economics, 2018, 157 (October 2016), 41–77.Xiong, Wei, “The Mandarin Model of Growth,” Working paper, 2019.Xu, Chenggang, “The Fundamental Institutions of China’s Reforms and Development,” Journalof Economic Literature, 2011, 49 (4), 1076–1151.Yao, Yang, “The political economy causes of China’s economic success,” China’s 40 Years ofReform and Development: 1978–2018, 2018, pp. 75–92.and Muyang Zhang, “Subnational leaders and economic growth: evidence from Chinesecities,” Journal of Economic Growth, 2015, 20, 405436.Zheng, Siqi, Matthew E. Kahn, Weizeng Sun, and Danglun Luo, “Incentives for China’surban mayors to mitigate pollution externalities: The role of the central government and publicenvironmentalism,” Regional Science and Urban Economics, 2014, 47, 61 – 71.79Appendix AAppendix to Chapter 2A.1 A model of a promotion tournamentOne way to think about China’s promotion tournament is as an incentive scheme.74 Toencourage leaders to exert effort in growing GDP, the goverment rewards the best-performingleaders with promotion. Here I focus on the prefecture-level promotion tournament. Suppose thatthe provincial government’s payoff is a function of the tax revenues remitted upwards from theprefecture governments competing in the tournament. In particular, assume that the provincialgovernment receives taxes equal to a share α of prefecture leader i’s growth, for a payoff αgi. Nextassume that economic growth is a function of a leader’s effort ei and an idiosyncratic shock εi:gi = ei + εi, where εi has a mean-zero distribution function F.The prefecture leader’s payoff is r if they are promoted and 0 otherwise (assuming commitmenton the part of the provincial government). The cost of effort is c(ei), where c′ > 0 and c′′ > 0. Theleader is promoted if αgi ≥ u¯, where u¯ ∼ U [−1/2ν, 1/2ν] is the growth performance of the nextbest competitor. The probability of promotion is given byP(αgi ≥ u¯) =∫[12+ να(ei + εi)]dF (εi) =12+ ναei,where∫εidF (εi) = 0.Hence, leader i chooses ei to maximize r(1/2 + ναei)− c(ei). Taking the first-order condition,and using c′′ > 0, we have a unique e∗i defined by rνα = c′(e∗i ). The main insight here is that theprobability of promotion is increasing in GDP growth. To show this, differentiate P(αgi ≥ u¯) withrespect to gi to get να > 0. Thus, if China is running a promotion tournament, we should observea positive correlation between relative GDP growth and promotion.A.2 Promotion definitionsA mayor is promoted if they take a position as a:• Promotion1: prefecture secretary74This section is based on Jia et al. (2015), who also provide a model of promotion as a screening device for thegovernment to select high ability leaders.80• Promotion2: Promotion1+ mayor in a sub-provincial city, higher-ranking position in theprovincial or central government, or a higher-ranking position in the Communist YouthLeague.• Promotion3: Promotion2+ vice-chairman, vice-secretary, chairman, or secretary of the Lead-ing Party Members Group in the provincial Local People’s Congress or Chinese People’sPolitical Consultative Conference.• Promotion4: Promotion3+ head of a provincial bureau.Unless noted otherwise, my results use Promotion2.81A.3 Results82Table A.1: LPM: results for tenure and education(1) (2) (3)GDP growth -0.034 -0.093 -0.059(0.085) (0.090) (0.109)Tenure 0.037∗∗∗ 0.036∗∗∗(0.006) (0.006)High school 0.000 0.000(.) (.)College 0.044 0.041(0.033) (0.031)Master’s 0.051 0.044(0.032) (0.030)Ph.D. 0.068∗∗ 0.065∗∗(0.034) (0.033)Age 0.053∗∗ 0.062∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.018 0.018(0.024) (0.023)Home prefecture -0.087∗∗∗ -0.068∗∗∗(0.018) (0.020)Connection -0.067∗∗∗ -0.065∗∗∗(0.020) (0.020)Initial GDP -0.022∗∗(0.009)Initial Population 0.020∗(0.011)Observations 5640 5175 5144Adjusted R2 0.080 0.122 0.124Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDPgrowth is a mayor’s cumulative average rel-ative growth rate over their term. Prefecture covariatesincludes dummy variables for prefecture type. Standarderrors clustered at the prefecture level.83Table A.2: LPM: clustering at province-year level(1) (2) (3)GDP growth -0.034 -0.091 -0.060(0.085) (0.086) (0.100)Age 0.047∗ 0.056∗∗(0.025) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.018(0.022) (0.022)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.017) (0.018)Connection -0.042∗ -0.041∗(0.021) (0.022)Initial GDP -0.017∗(0.010)Initial Population 0.018∗(0.011)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDPgrowth is a mayor’s cumulative average rela-tive growth rate over their term. Mayor covariates includedummy variables for tenure and education categories. Pre-fecture covariates includes dummy variables for prefecturetype. Standard errors clustered at the province-year level.84Table A.3: LPM: clustering at province level(1) (2) (3)GDP growth -0.034 -0.091 -0.060(0.063) (0.059) (0.074)Age 0.047∗ 0.056∗∗(0.023) (0.022)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.018(0.022) (0.021)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.020) (0.017)Connection -0.042∗∗ -0.041∗∗(0.016) (0.017)Initial GDP -0.017(0.011)Initial Population 0.018∗(0.010)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDPgrowth is a mayor’s cumulative average rela-tive growth rate over their term. Mayor covariates includedummy variables for tenure and education categories. Pre-fecture covariates includes dummy variables for prefecturetype. Standard errors clustered at the province level.85Figure A.1: Heterogeneity by yearNote: Coefficients are from baseline regression with GDP growth interacted with year dummies. Omitted year is1998.86Table A.4: Adding covariates in series(1) (2) (3) (4) (5) (6) (7) (8) (9) (10)GDP growth -0.034 -0.029 -0.051 -0.082 -0.070 -0.074 -0.091 -0.101 -0.079 -0.060(0.085) (0.085) (0.083) (0.087) (0.089) (0.089) (0.089) (0.090) (0.108) (0.108)Age 0.036∗ 0.032 0.055∗∗ 0.056∗∗ 0.047∗ 0.047∗ 0.061∗∗ 0.058∗∗ 0.056∗∗(0.022) (0.022) (0.024) (0.025) (0.024) (0.024) (0.025) (0.025) (0.025)Age squared -0.000∗ -0.000 -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗(0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Sex 0.012 0.008 0.010 0.018 0.017 0.017 0.020 0.018(0.021) (0.024) (0.024) (0.024) (0.024) (0.024) (0.024) (0.024)Home prefecture -0.081∗∗∗ -0.083∗∗∗ -0.083∗∗∗ -0.085∗∗∗ -0.065∗∗∗(0.018) (0.018) (0.018) (0.018) (0.019)Political connection -0.042∗∗ -0.042∗∗ -0.042∗∗ -0.041∗∗(0.020) (0.020) (0.020) (0.020)Initial GDP -0.000 -0.010 -0.017∗(0.008) (0.009) (0.009)Initial Population 0.019∗ 0.018∗(0.011) (0.011)Observations 5640 5565 5347 5345 5244 5184 5172 5161 5141 5141Province-year FE Yes Yes Yes Yes Yes Yes Yes Yes Yes YesTenure No No No Yes Yes Yes Yes Yes Yes YesEducation No No No No Yes Yes Yes Yes Yes YesPrefecture type No No No No No No No No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: the coefficient on Growth will be different if the order of covariates is different. See Gelbach (2016).87Table A.5: GDP growth above the target(1) (2) (3) (4) (5) (6) (7) (8) (9)Above target 0.009 -0.005 -0.003(0.011) (0.012) (0.012)Above by 3pp -0.017 -0.019 -0.015(0.011) (0.012) (0.013)Distance to target 0.032 -0.061 0.005(0.080) (0.086) (0.107)Age 0.048∗ 0.056∗∗ 0.047∗ 0.055∗∗ 0.048∗∗ 0.056∗∗(0.024) (0.025) (0.024) (0.025) (0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗(0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Gender 0.017 0.018 0.017 0.018 0.017 0.018(0.024) (0.024) (0.024) (0.024) (0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗ -0.083∗∗∗ -0.065∗∗∗ -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019) (0.018) (0.019) (0.018) (0.019)Political connection -0.041∗∗ -0.041∗∗ -0.041∗∗ -0.041∗∗ -0.042∗∗ -0.041∗∗(0.020) (0.020) (0.020) (0.020) (0.020) (0.020)Initial GDP -0.018∗ -0.017∗ -0.018∗(0.009) (0.009) (0.009)Initial Population 0.019∗ 0.018∗ 0.019∗(0.010) (0.011) (0.011)Observations 5640 5172 5141 5640 5172 5141 5640 5172 5141Adjusted R2 0.080 0.126 0.128 0.080 0.126 0.128 0.080 0.126 0.128Province-year FE Yes Yes Yes Yes Yes Yes Yes Yes YesMayor covariates No Yes Yes No Yes Yes No Yes YesPrefecture covariates No No Yes No No Yes No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Above target and Above by 3pp are indicator variables for a mayor being above the provincial GDP growth target byany amount, and by 3 percentage points, respectively. Distance to target is calculated as cumulative average GDP growthminus the annual target. Standard errors clustered at the prefecture level.88Table A.6: Consecutive years above the growth target(1) (2) (3) (4) (5) (6)Above twice 0.078∗∗∗ 0.004 0.004(0.011) (0.015) (0.015)Above thrice 0.102∗∗∗ 0.002 0.003(0.014) (0.020) (0.020)Age 0.048∗∗ 0.057∗∗ 0.048∗∗ 0.056∗∗(0.024) (0.025) (0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗(0.000) (0.000) (0.000) (0.000)Gender 0.017 0.018 0.017 0.018(0.024) (0.024) (0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗ -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019) (0.018) (0.019)Political connection -0.041∗∗ -0.041∗∗ -0.041∗∗ -0.041∗∗(0.020) (0.020) (0.020) (0.020)Initial GDP -0.018∗ -0.018∗(0.009) (0.009)Initial Population 0.019∗ 0.019∗(0.010) (0.010)Observations 5640 5172 5141 5640 5172 5141Adjusted R2 0.088 0.126 0.128 0.091 0.126 0.128Province-year FE Yes Yes Yes Yes Yes YesMayor covariates No Yes Yes No Yes YesPrefecture covariates No No Yes No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Above twice and Above thrice are indicator variables for a mayor being above the provin-cial GDP growth target two and three years in a row, respectively. Standard errors clusteredat the prefecture level.89Table A.7: Consecutive years below the growth target(1) (2) (3) (4) (5) (6)Below twice 0.054∗∗∗ 0.009 0.009(0.014) (0.017) (0.017)Below thrice 0.109∗∗∗ 0.024 0.023(0.022) (0.026) (0.026)Age 0.047∗ 0.056∗∗ 0.047∗ 0.055∗∗(0.024) (0.025) (0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗ -0.001∗∗ -0.001∗∗(0.000) (0.000) (0.000) (0.000)Gender 0.017 0.018 0.017 0.018(0.024) (0.024) (0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗ -0.084∗∗∗ -0.065∗∗∗(0.018) (0.019) (0.018) (0.019)Political connection -0.041∗∗ -0.041∗∗ -0.042∗∗ -0.041∗∗(0.020) (0.020) (0.020) (0.020)Initial GDP -0.018∗ -0.018∗(0.009) (0.009)Initial Population 0.019∗ 0.019∗(0.010) (0.010)Observations 5640 5172 5141 5640 5172 5141Adjusted R2 0.082 0.126 0.128 0.085 0.126 0.128Province-year FE Yes Yes Yes Yes Yes YesMayor covariates No Yes Yes No Yes YesPrefecture covariates No No Yes No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Below twice and Below thrice are indicator variables for a mayor being below the provin-cial GDP growth target two and three years in a row, respectively. Standard errors clusteredat the prefecture level.90Table A.8: Does meritocration promotion vary by prefecture type?(1) (2) (3)GDP growth -0.023 -0.138 -0.116(0.095) (0.101) (0.120)Type: prefecture 0.018 -0.012 -0.042(0.027) (0.032) (0.035)Type: Autonomous prefecture -0.097∗∗∗ -0.087∗∗∗ -0.094∗∗∗(0.013) (0.019) (0.021)Growth × prefecture 0.110 0.681 0.440(0.422) (0.517) (0.518)Growth × autonomous 0.110 0.376 0.377(0.259) (0.238) (0.241)Age 0.045∗ 0.056∗∗(0.024) (0.025)Age squared -0.000∗ -0.001∗∗(0.000) (0.000)Gender 0.016 0.018(0.024) (0.024)Home prefecture -0.065∗∗∗ -0.067∗∗∗(0.019) (0.019)Political connection -0.041∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.017∗(0.009)Initial Population 0.018∗(0.011)Observations 5640 5172 5141Adjusted R2 0.083 0.128 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Omitted group is prefecture-level cities. Standard errors clus-tered at the prefecture level.91Table A.9: Dropping mayors promoted in first year(1) (2) (3)GDP growth 0.001 -0.047 -0.027(0.077) (0.080) (0.097)Age 0.056∗∗∗ 0.070∗∗∗(0.020) (0.020)Age squared -0.001∗∗∗ -0.001∗∗∗(0.000) (0.000)Sex 0.002 0.003(0.022) (0.022)Home prefecture -0.082∗∗∗ -0.067∗∗∗(0.016) (0.018)Political connection -0.041∗∗ -0.041∗∗(0.019) (0.019)Initial GDP -0.011(0.009)Initial Population 0.017∗(0.010)Observations 5472 5013 4982Adjusted R2 0.070 0.167 0.168Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is a mayor’s cumulative average rel-ative growth rate over their term. Mayor covariates in-clude dummy variables for tenure and education cate-gories. Standard errors clustered at the prefecture level.Excluding mayors who are promoted after serving one yearin office.92Table A.10: Interaction with autonomous dummy(1) (2) (3)GDP growth -0.005 -0.102 -0.064(0.112) (0.122) (0.124)Growth × Autonomous -0.103 0.037 0.022(0.139) (0.148) (0.228)Age 0.047∗ 0.056∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.018(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019)Political connection -0.042∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.018∗(0.009)Initial Population 0.018∗(0.011)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is a mayor’s cumulative average rela-tive growth rate over their term. Mayor covariates includedummy variables for tenure and education categories. Stan-dard errors clustered at the prefecture level. Autonomousregions: Tibet, Xinjiang, Inner Mongolia, Ningxia, andGuangxi.93Table A.11: Growth relative to predecessor’s average(1) (2) (3)GDP growth 0.057 0.027 0.034(0.070) (0.082) (0.096)Age 0.079∗∗ 0.075∗∗(0.034) (0.034)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.005 0.006(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.061∗∗∗(0.020) (0.021)Connection -0.037∗ -0.037∗(0.021) (0.021)Initial GDP -0.015(0.010)Initial Population 0.013(0.011)Observations 4875 4647 4635Adjusted R2 0.078 0.122 0.125Mayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is a mayor’s cumulative average rel-ative growth rate over their term; growth is calculatedrelative to a mayor’s predecessor’s average growth rate(through subtraction). Mayor covariates include dummyvariables for tenure and education categories. Standarderrors clustered at the prefecture level.94Table A.12: Growth relative to provincial average and predecessor’s average(1) (2) (3)GDP growth 0.012 -0.000 -0.002(0.072) (0.084) (0.098)Age 0.079∗∗ 0.074∗∗(0.034) (0.034)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.005 0.006(0.024) (0.024)Home prefecture -0.084∗∗∗ -0.061∗∗∗(0.020) (0.021)Connection -0.038∗ -0.038∗(0.021) (0.021)Initial GDP -0.016(0.010)Initial Population 0.014(0.011)Observations 4875 4647 4635Adjusted R2 0.078 0.122 0.125Mayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is a mayor’s cumulative average rela-tive growth rate over their term; growth is calculated rel-ative to the provincial average and the mayor’s predeces-sor’s average growth rate (through subtraction). Mayorcovariates include dummy variables for tenure and educa-tion categories. Standard errors clustered at the prefec-ture level.95Table A.13: Indicator variable for maximum growth(1) (2) (3)Maximum growth -0.025 -0.021 -0.021(0.017) (0.018) (0.018)Age 0.047∗ 0.056∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.017(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019)Political connection -0.042∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.018∗(0.009)Initial Population 0.018∗(0.010)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Maximum growth is a dummy variable for a mayorhaving the highest growth in a province-year. Mayor co-variates include dummy variables for tenure and educa-tion categories. Standard errors clustered at the prefec-ture level.96Table A.14: Indicator variable for growth above median(1) (2) (3)Growth > median -0.004 -0.009 -0.008(0.010) (0.010) (0.010)Age 0.047∗ 0.056∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.018(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019)Political connection -0.042∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.018∗(0.009)Initial Population 0.018∗(0.010)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Growth > median is a dummy variable for amayor having growth higher than the province-year me-dian. Mayor covariates include dummy variables for tenureand education categories. Standard errors clustered at theprefecture level.97Table A.15: Indicator variable for growth quartiles(1) (2) (3)Growth: 2nd quartile 0.006 0.011 0.011(0.013) (0.014) (0.014)Growth: 3rd quartile 0.006 0.003 0.004(0.014) (0.014) (0.014)Growth: 4th quartile -0.010 -0.011 -0.011(0.013) (0.014) (0.014)Age 0.047∗ 0.055∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.016 0.017(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.064∗∗∗(0.018) (0.019)Political connection -0.042∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.018∗(0.009)Initial Population 0.017∗(0.010)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Growth quartiles are dummy variables calculated foreach province-year. Mayor covariates include dummy vari-ables for tenure and education categories. Standard errorsclustered at the prefecture level.98Table A.16: Calculate provincial average excluding i(1) (2) (3)GDP growth -0.037 -0.087 -0.063(0.075) (0.079) (0.098)Age 0.047∗ 0.056∗∗(0.024) (0.025)Age squared -0.001∗∗ -0.001∗∗(0.000) (0.000)Sex 0.017 0.018(0.024) (0.024)Home prefecture -0.083∗∗∗ -0.065∗∗∗(0.018) (0.019)Political connection -0.042∗∗ -0.041∗∗(0.020) (0.020)Initial GDP -0.017∗(0.009)Initial Population 0.018∗(0.011)Observations 5640 5172 5141Adjusted R2 0.080 0.126 0.128Province-year FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: GDP growth is calculated relative to the provincialaverage, where the latter is computed excluding observa-tion i; this variable is then used to calculate cumulativerelative average growth. Mayor covariates include dummyvariables for tenure and education categories. Standarderrors clustered at the prefecture level.99Table A.17: Chen and Kung (2019): prefecture secretariesLPM Logit Ordered logit(1) (2) (3) (4) (5) (6)Annual growth 0.055 1.123 0.731(0.076) (1.474) (0.784)Cumulative average growth 0.048 0.702 0.388(0.080) (1.672) (0.905)Age 0.051∗ 0.051∗ 0.921 0.949∗ 2.646∗∗∗ 2.654∗∗∗(0.029) (0.029) (0.577) (0.569) (0.378) (0.378)Age squared -0.001∗ -0.001∗ -0.010∗ -0.010∗ -0.027∗∗∗ -0.027∗∗∗(0.000) (0.000) (0.006) (0.005) (0.004) (0.004)Sex 0.012 0.012 0.347 0.354 -0.328 -0.324(0.029) (0.029) (0.491) (0.486) (0.419) (0.419)Education 0.000 0.000 -0.003 -0.003 -0.031 -0.031(0.002) (0.002) (0.038) (0.038) (0.026) (0.026)Connections 0.003 0.003 0.063 0.051 0.264 0.266(0.017) (0.017) (0.270) (0.269) (0.220) (0.219)Initial GDP 0.036∗∗∗ 0.035∗∗∗ 0.635∗∗∗ 0.629∗∗∗ 0.450∗∗∗ 0.447∗∗∗(0.006) (0.006) (0.106) (0.105) (0.074) (0.074)Tenure 0.025∗∗∗ 0.025∗∗∗ 0.402∗∗∗ 0.399∗∗∗ 0.004 0.003(0.004) (0.004) (0.068) (0.067) (0.060) (0.060)Observations 3009 3009 1465 1465 3023 3023Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Sample covers 2004-2014. Regression model: Promotionijpt = β Growthijpt + λXijpt + ijpt.Province-year fixed effects. Standard errors clustered at the prefecture level (LPM and ordered logit)and province-year level (logit). Note that Tenure measures years in office as observed in the data, ratherthan actual years in office; the authors do not include a tenure variable. Similarly, Initial GDP is de-fined using a leader’s first observed year in office.100Table A.18: Yao and Zhang (2015): prefecture secretariesLPM Logit(1) (2) (3) (4)Annual growth 0.073 0.628(0.063) (0.609)Cumulative average growth -0.124 -1.303(0.087) (0.942)Age 0.026 0.029 0.242 0.285(0.025) (0.025) (0.329) (0.333)Age squared -0.000 -0.000 -0.003 -0.003(0.000) (0.000) (0.003) (0.003)Tenure 0.021∗∗∗ 0.021∗∗∗ 0.229∗∗∗ 0.232∗∗∗(0.003) (0.003) (0.031) (0.031)Provincial experience 0.032∗∗∗ 0.030∗∗∗ 0.377∗∗∗ 0.360∗∗∗(0.011) (0.011) (0.140) (0.140)Initial GDP 0.028∗∗∗ 0.030∗∗∗ 0.324∗∗∗ 0.340∗∗∗(0.009) (0.009) (0.106) (0.106)Observations 3756 3756 2445 2445Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Sample covers 1998-2010. Regression model: Promotionijpt =β Growthijpt + λXijpt + ijpt. Province-year fixed effects. Standard errorsclustered at the prefecture level (LPM) and province-year level (logit).101Table A.19: Li et al. (2019): prefecture secretariesLPM Logit(1) (2) (3) (4)Annual growth 0.100 1.853(0.182) (2.078)Cumulative average growth 0.226 4.918∗(0.197) (2.569)Age -0.037 -0.037 -0.450 -0.445(0.032) (0.032) (0.404) (0.404)Age squared 0.000 0.000 0.004 0.004(0.000) (0.000) (0.004) (0.004)Tenure 0.043∗∗∗ 0.043∗∗∗ 0.402∗∗∗ 0.399∗∗∗(0.005) (0.005) (0.042) (0.042)Education 0.032 0.032 0.465 0.478(0.022) (0.022) (0.332) (0.339)Observations 3290 3290 1976 1976Adjusted R2 0.141 0.141Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Sample covers 2003-2014. Regression model: Promotionijpt =β Growthijpt + λXijpt + ijpt. Province-year fixed effects. Standard errorsclustered at the prefecture level (LPM) and province-year level (logit).102Table A.20: Landry et al. (2018): prefecture secretariesLPM Logit(1) (2) (3) (4)Annual growth -0.008 -0.062(0.005) (0.074)Cumulative average growth -0.006 -0.113(0.006) (0.088)Age -0.076∗∗ -0.077∗∗ -0.721∗∗ -0.715∗∗(0.031) (0.031) (0.330) (0.331)Age squared 0.001∗∗ 0.001∗∗ 0.007∗∗ 0.007∗∗(0.000) (0.000) (0.003) (0.003)Tenure 0.038∗∗∗ 0.038∗∗∗ 0.328∗∗∗ 0.330∗∗∗(0.006) (0.006) (0.071) (0.071)Connections 0.008 0.008 -0.091 -0.093(0.014) (0.014) (0.286) (0.286)Observations 2487 2487 1465 1465Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Sample covers 1999-2007. Regression model: Promotionijpt =βGrowthijpt+λXijpt+ijpt. Province-year and prefecture type fixed effects.Standard errors clustered at the prefecture level (LPM) and province-yearlevel (logit).103Appendix BAppendix to Chapter 3104B.1 Literature characteristics105Table B.1: Article characteristicsYao and Zhang(2015)Li et al.(2019)Chen and Kung(2019)Landry et al.(2018)Lorentzen and Lu(2018)Sampleperiod1998-2010 2003-2014 2004-2014 1999-2007 2006-2012Method AKM leader effect MLELPM,ordered probitLPM LPMDatalevelAnnual Annual Annual Spell SpellMayor vs.secretaryPooled Pooled Separate Separate PooledGDP growth AnnualAnnual,cumulativeaverageAnnual Average AverageReanalysisRe-estimate leadereffects droppingsome controlsLPM, logisticMy promotiondataAnnual data withcumulative averageGDP growthMy promotion data;annual data withcumulative averageGDP growth106B.2 Yao and Zhang (2015)107Figure B.1: Yao and Zhang (2015), Table 4108Figure B.2: Yao and Zhang (2015), Table 4 (continued)109Figure B.3: Yao and Zhang (2015), Table 5110Figure B.4: Yao and Zhang (2015), Table 5 (continued)111Figure B.5: Yao and Zhang (2015), Table 6112Figure B.6: Yao and Zhang (2015), Table 6 (continued)113Figure B.7: Yao and Zhang (2015), Table 7114Figure B.8: Yao and Zhang (2015), Table 7 (continued)115Table B.2: Reanalysis of Table 5, Yao and Zhang (2015)(1) (2) (3) (4) (5) (6)Threshold: 49 Threshold: 50 Threshold: 51 Threshold: 52Leader effect 0.105 -1.712 -0.197 -0.143 -0.323 -0.134(0.191) (2.521) (0.257) (0.235) (0.217) (0.201)Leader effect × Age 0.036(0.051)Age -0.054∗∗∗ -0.054∗∗∗(0.005) (0.005)Provincial experience 0.161∗∗∗ 0.162∗∗∗ 0.160∗∗∗ 0.164∗∗∗ 0.172∗∗∗ 0.169∗∗∗(0.043) (0.043) (0.043) (0.043) (0.043) (0.042)Tenure 0.028∗∗ 0.028∗∗ 0.003 0.006 0.012 0.016(0.011) (0.011) (0.012) (0.012) (0.012) (0.011)Leader effect × (Age > threshold) 0.533 0.464 0.956∗∗ 0.530(0.393) (0.395) (0.386) (0.439)Age > threshold -0.261∗∗∗ -0.275∗∗∗ -0.348∗∗∗ -0.422∗∗∗(0.041) (0.040) (0.042) (0.047)Observations 4189 4189 4189 4189 4189 4189Adjusted R2Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Ordered probit model. Dependent variable is an ordered categorical promotion variable. Province and year fixed effects.Standard errors are clustered at the prefecture level.116Table B.3: Reanalysis of Table 6, Yao and Zhang (2015)(1) (2) (3) (4) (5)Threshold: 49 Threshold: 50 Threshold: 51 Threshold: 52Leader effect -0.588 -0.035 -0.015 -0.071 -0.017(0.640) (0.096) (0.091) (0.086) (0.082)Leader effect × Age 0.012(0.013)Age -0.006∗∗∗(0.001)Provincial experience 0.051∗∗∗ 0.051∗∗∗ 0.052∗∗∗ 0.053∗∗∗ 0.052∗∗∗(0.012) (0.012) (0.012) (0.012) (0.012)Tenure 0.025∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.023∗∗∗ 0.024∗∗∗(0.003) (0.003) (0.003) (0.003) (0.003)Leader effect × (Age > threshold) 0.112 0.082 0.224∗∗ 0.110(0.111) (0.110) (0.111) (0.116)Age > threshold -0.044∗∗∗ -0.037∗∗∗ -0.042∗∗∗ -0.048∗∗∗(0.012) (0.012) (0.012) (0.012)Observations 5403 5403 5403 5403 5403Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Joint estimation of linear-linear model. Dependent variable is a dummy promotion variable. Province and yearfixed effects. The original Yao and Zhang code incorrectly used a categorical promotion variable, instead of a dummyvariable; however, this does not substantively affect the results.117Table B.4: Reanalysis of Table 7, Yao and Zhang (2015)(1) (2) (3) (4) (5)Threshold: 49 Threshold: 50 Threshold: 51 Threshold: 52Leader effect -1.714 -0.203 -0.145 -0.325 -0.137(2.367) (0.357) (0.338) (0.320) (0.306)Leader effect × Age 0.036(0.047)Age -0.054∗∗∗(0.005)Provincial experience 0.162∗∗∗ 0.160∗∗∗ 0.164∗∗∗ 0.172∗∗∗ 0.169∗∗∗(0.045) (0.045) (0.045) (0.045) (0.045)Tenure 0.028∗∗ 0.003 0.006 0.012 0.016(0.011) (0.011) (0.011) (0.011) (0.011)Leader effect × (Age > threshold) 0.543 0.467 0.958∗∗ 0.538(0.413) (0.409) (0.417) (0.435)Age > threshold -0.261∗∗∗ -0.275∗∗∗ -0.348∗∗∗ -0.422∗∗∗(0.044) (0.044) (0.045) (0.047)Observations 5403 5403 5403 5403 5403Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Joint estimation of linear-ordered-probit model. Dependent variable is an ordered categorical promotion vari-able. Province and year fixed effects.118B.3 Li et al. (2019)Table B.5: Replication of Table 5 (Li et al., 2019): logit model(1) (2) (3) (4)Growth rate (annual) 0.172 -15.56∗(1.315) (9.205)Annual growth × target 148.5∗(83.50)Growth rate (cumulative) 1.766 -8.445(1.802) (10.48)Cumulative growth × target 98.11(102.5)Observations 4635 4635 4635 4635Province-year FE Yes Yes Yes YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Logit estimation of Promotionijpt = β1Growthijpt +β2Growthijpt × Targetpt + λXijpt + ijpt. Province-year fixed ef-fects. Standard errors clustered at the province-year level. Covariates:mayor/secretary FE, Age and Age2, Tenure, and Education.119Figure B.9: Sample size: Li et al. (2019)Note: There are 333 prefecture-level jurisdictions in China.120B.4 Chen and Kung (2019)Table B.6: Verification of Table IX, Chen and Kung (2019)(1) (2) (3) (4)Princeling Purchase (=1) 0.093 -0.008(0.108) (0.011)Princeling Discounts 0.012(0.008)Area of Land Purchased 0.000(0.047)Factional Ties -0.027 -0.014 -0.021 -0.026(0.101) (0.010) (0.101) (0.101)GDP Growth 2.798∗∗∗ 0.365∗∗∗ 2.726∗∗∗ 2.771∗∗∗(0.761) (0.076) (0.761) (0.770)Tax Revenue Growth 1.097∗∗ 0.064 1.087∗∗ 1.074∗∗(0.523) (0.052) (0.523) (0.524)Observations 2569 2569 2568 2568Adjusted R2 0.374Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Direct replication of Columns 7-10 in Table IX in Chen and Kung(2019). Dependent variable is Promotion. Prefecture and year fixed ef-fects. Standard errors are not clustered. Covariates: log GDP per capita,log population, Age and Age2, and Education.121Table B.7: Replication of Table IX, Chen and Kung (2019): corrected promotion variable(1) (2) (3) (4)Princeling Purchase (=1) 0.042 -0.018∗∗(0.127) (0.009)Princeling Discounts 0.007(0.009)Area of Land Purchased 0.025(0.054)Factional Ties 0.135 -0.003 0.140 0.148(0.119) (0.008) (0.119) (0.119)GDP Growth 2.836∗∗∗ 0.223∗∗∗ 2.783∗∗∗ 2.759∗∗∗(0.873) (0.062) (0.875) (0.885)Tax Revenue Growth 0.845 0.008 0.841 0.911(0.594) (0.043) (0.594) (0.596)Observations 2565 2565 2564 2564Adjusted R2 0.050Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Reanalysis of Columns 7-10 in Table IX in Chen and Kung (2019).Dependent variable is Promotion from Chen and Kung, with data errorscorrected. Prefecture and year fixed effects. Standard errors are not clus-tered. Covariates: log GDP per capita, log population, Age and Age2,and Education.Table B.8: Replication of Table IX, Chen and Kung (2019): promotion definition 1Ordered probit LPM(1) (2)GDP Growth -0.346 -0.062(0.752) (0.130)Observations 2549 2549Adjusted R2 0.004Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Reanalysis of mayor results from Ta-ble IX in Chen and Kung (2019). Dependentvariable is Promotion from my data, usingdefinition 1. Prefecture and year fixed ef-fects. Standard errors clustered at the prefec-ture level. Covariates: tax revenue growth,log GDP per capita, and log population.122Table B.9: Replication of Table IX, Chen and Kung (2019): promotion definition 3Ordered probit LPM(1) (2)GDP Growth -0.432 -0.075(0.689) (0.133)Observations 2549 2549Adjusted R2 0.011Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Reanalysis of mayor results from Ta-ble IX in Chen and Kung (2019). Dependentvariable is Promotion from my data, usingdefinition 3. Prefecture and year fixed ef-fects. Standard errors clustered at the prefec-ture level. Covariates: tax revenue growth,log GDP per capita, and log population.Table B.10: Replication of Table IX, Chen and Kung (2019): promotion definition 4Ordered probit LPM(1) (2)GDP Growth 0.238 0.086(0.672) (0.148)Observations 2549 2549Adjusted R2 0.017Standard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Reanalysis of mayor results from Ta-ble IX in Chen and Kung (2019). Dependentvariable is Promotion from my data, usingdefinition 4. Prefecture and year fixed ef-fects. Standard errors clustered at the prefec-ture level. Covariates: tax revenue growth,log GDP per capita, and log population.123B.5 Landry et al. (2018)124Table B.11: Direct replication: province leadersSecretary Governor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.169∗∗ 0.136 0.168 0.087 -0.190∗∗∗ -0.179∗∗∗ -0.318∗∗∗ -0.283∗∗∗(0.082) (0.080) (0.137) (0.124) (0.067) (0.064) (0.114) (0.101)Connection -0.001 -0.016 -0.001 -0.007 0.237∗ 0.216 0.258∗ 0.231∗(0.082) (0.059) (0.086) (0.067) (0.133) (0.134) (0.130) (0.131)Growth × Connection 0.002 0.079 0.196 0.159(0.158) (0.160) (0.161) (0.163)Observations 65 65 65 65 67 67 67 67Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Direct replication of Columns 1-4 in Tables 5-6 from Landry et al. (2018). Year fixed effects. Standard errorsclustered at the province level. The governor results have one fewer observation than in the original, because reghdfedrops one singleton observation.125Table B.12: Direct replication: prefecture leadersSecretary Mayor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.025 0.016 0.017 0.010 0.020 0.017 0.003 0.001(0.032) (0.034) (0.042) (0.042) (0.032) (0.032) (0.043) (0.045)Connection -0.016 0.030 -0.015 0.030 0.035 0.041 0.036 0.041(0.042) (0.052) (0.043) (0.052) (0.039) (0.041) (0.039) (0.041)Growth × Connection 0.020 0.015 0.038 0.037(0.064) (0.066) (0.061) (0.061)Observations 663 605 663 605 772 725 772 725Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Direct replication of Columns 5-8 in Tables 5-6 from Landry et al. (2018). Province and year fixedeffects. Standard errors clustered at the prefecture level. Each regression has one fewer observation than inthe original, because reghdfe drops one singleton observation.126Table B.13: Direct replication: county leadersSecretary Mayor(1) (2) (3) (4) (5) (6) (7) (8)GDP growth 0.041∗∗∗ 0.044∗∗∗ 0.048∗∗∗ 0.047∗∗∗ 0.035∗∗∗ 0.037∗∗∗ 0.041∗∗∗ 0.046∗∗∗(0.011) (0.014) (0.014) (0.017) (0.010) (0.012) (0.013) (0.016)Connection -0.056∗∗∗ -0.014 -0.056∗∗∗ -0.014 0.048∗∗∗ 0.033∗ 0.048∗∗∗ 0.032∗(0.018) (0.023) (0.018) (0.023) (0.015) (0.019) (0.015) (0.019)Growth × Connection -0.020 -0.010 -0.014 -0.022(0.024) (0.030) (0.020) (0.023)Observations 4648 3438 4648 3438 5623 3844 5623 3844Adjusted R2 0.096 0.094 0.096 0.094 0.040 0.050 0.040 0.050Politician covariates No Yes No Yes No Yes No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Direct replication of Columns 5-8 in Tables 5-6 from Landry et al. (2018). Prefecture and year fixed effects.Standard errors clustered at the county level. The sample size is smaller than in the original, because reghdfe dropssingleton observations.127B.6 Lorentzen and Lu (2018)Figure B.10: Lorentzen and Lu (2018), Table 4128Table B.14: Nonmeritocratic promotion in Tiger provinces? Promotion definition 1(1) (2) (3)GDP growth 1.322∗ 1.415∗ 1.651∗∗(0.722) (0.724) (0.757)Growth × Tiger province -1.515 -1.739 -1.429(1.192) (1.199) (1.265)Age 0.526∗∗∗ 0.555∗∗∗(0.119) (0.119)Age squared -0.005∗∗∗ -0.006∗∗∗(0.001) (0.001)Sex 0.062 0.069(0.093) (0.088)Home prefecture -0.002 0.018(0.117) (0.113)Connection -0.011 0.003(0.064) (0.062)Initial GDP 0.011(0.041)Initial Population 0.110∗∗(0.049)Observations 423 416 416Adjusted R2 0.049 0.108 0.130Province FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: spell-level data for mayors with spells starting after 2005and ending before 2013. Tiger province is a dummy variablefor Shanxi, Jiangxi, and Sichuan. Standard errors clustered atthe prefecture level.129Table B.15: Nonmeritocratic promotion in Tiger provinces? Promotion definition 3(1) (2) (3)GDP growth 0.404 0.484 0.721(0.696) (0.767) (0.744)Growth × Tiger province -0.186 -0.452 -0.017(1.356) (1.391) (1.441)Age 0.272∗∗ 0.294∗∗(0.134) (0.132)Age squared -0.003∗∗ -0.003∗∗(0.001) (0.001)Sex 0.114 0.132(0.089) (0.086)Home prefecture -0.134 -0.206∗(0.111) (0.110)Connection -0.050 -0.040(0.065) (0.064)Initial GDP 0.069∗(0.039)Initial Population 0.102∗∗(0.046)Observations 423 416 416Adjusted R2 0.020 0.050 0.077Province FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: spell-level data for mayors with spells starting after2005 and ending before 2013. Tiger province is a dummyvariable for Shanxi, Jiangxi, and Sichuan. Standard errorsclustered at the prefecture level.130Table B.16: Nonmeritocratic promotion in Tiger provinces? Promotion definition 4(1) (2) (3)GDP growth 0.303 0.394 0.487(0.614) (0.628) (0.624)Growth × Tiger province -0.494 -0.575 -0.298(1.398) (1.266) (1.303)Age 0.352∗∗ 0.373∗∗(0.149) (0.149)Age squared -0.004∗∗ -0.004∗∗(0.001) (0.001)Sex 0.073 0.081(0.079) (0.079)Home prefecture 0.016 0.003(0.075) (0.083)Connection -0.040 -0.034(0.055) (0.055)Initial GDP 0.042(0.032)Initial Population 0.053(0.039)Observations 423 416 416Adjusted R2 -0.002 0.016 0.020Province FE Yes Yes YesMayor covariates No Yes YesPrefecture covariates No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: spell-level data for mayors with spells starting after2005 and ending before 2013. Tiger province is a dummyvariable for Shanxi, Jiangxi, and Sichuan. Standard errorsclustered at the prefecture level.131Table B.17: Tiger provinces: cumulative average GDP growth(1) (2) (3) (4) (5) (6)GDP growth -0.129 -0.061 -0.002 -0.178 -0.231 -0.156(0.148) (0.152) (0.158) (0.211) (0.201) (0.200)Growth × Tiger province 0.028 0.200 0.229 0.103 0.239 0.261(0.330) (0.316) (0.327) (0.381) (0.376) (0.376)Age 0.175∗∗∗ 0.181∗∗∗ 0.236∗∗∗ 0.247∗∗∗(0.041) (0.041) (0.075) (0.075)Age squared -0.002∗∗∗ -0.002∗∗∗ -0.002∗∗∗ -0.003∗∗∗(0.000) (0.000) (0.001) (0.001)Sex 0.014 0.017 0.013 0.008(0.033) (0.033) (0.043) (0.044)Home prefecture -0.082∗∗∗ -0.072∗∗ -0.081∗∗ -0.070∗(0.028) (0.030) (0.040) (0.042)Connection -0.037 -0.037 -0.025 -0.020(0.030) (0.030) (0.049) (0.049)Initial GDP -0.032∗∗ 0.017(0.013) (0.022)Initial Population 0.041∗∗∗ 0.008(0.016) (0.023)Observations 2198 2164 2156 1062 1060 1060Adjusted R2 0.094 0.169 0.170 0.282 0.300 0.299Province-year FE Yes Yes Yes Yes Yes YesMayor covariates No Yes Yes No Yes YesPrefecture covariates No No Yes No No YesStandard errors in parentheses∗ p < 0.1, ∗∗ p < 0.05, ∗∗∗ p < 0.01Note: Columns (1)-(3) restrict the sample to 2006-2012. Columns (4)-(6) further restrict the sam-ple to mayors with spells starting after 2005 and ending before 2013. Tiger province is a dummyvariable for Shanxi, Jiangxi, and Sichuan. Standard errors clustered at the prefecture level.132Appendix CAppendix to Chapter 4C.1 Persistence of bunchingIs bunching status persistent over time? Persistence speaks to whether bunching-above is simplyrandom, in contrast to our hypothesis, or whether some underlying characteristic of the firm isdetermining their ability to access the preferential tax rate. Persistence could arise if tax collectorsdo not easily update their initial judgments of a firms eligibility, and therefore repeatedly inhibitthe same firms from accessing the preferential rates. Similarly, the signal a firm receives from taxcollectors regarding their perceived eligibility in one period may persist into future periods. Westart with graphical evidence documenting the patterns of persistence. Figure C.1 follows cohortsof bunchers into the following year. As an example, Panel A restricts to firms in 2010 with reportedincome within a 5 percent bandwidth around the micro enterprise notch, divides these firms intoabove- and below- bunchers, then plots their distribution of income in the following year. Firmsbunching above in 2010 were substantially more likely to do so again in 2011. Panel B showsthe same pattern for the 2011 to 2012 transition, despite the fact that the micro enterprise notchwas increased from 30,000 to 60,000 in 2012. Firms that bunching above the 30,000 notch aresubstantially more likely to bunch above the 60,000 notch. Panels C and D further corroboratethis pattern.133Figure C.1: Persistence of bunching status(a) Persistence from 2010 to 20110.02.04.06.08Frequency0 20000 40000 60000 80000 100000Taxable Income in 2011Bunched Below in 2010 Bunched Above in 2010(b) Persistence from 2011 to 20120.01.02.03.04Frequency0 20000 40000 60000 80000 100000Taxable Income in 2012Bunched Below in 2011 Bunched Above in 2011(c) Persistence from 2012 to 20130.05.1.15Frequency40000 60000 80000 100000 120000 140000Taxable Income in 2013Bunched Below in 2012 Bunched Above in 2012(d) Persistence from 2013 to 20140.01.02.03.04Frequency40000 60000 80000 100000 120000 140000Taxable Income in 2014Bunched Below in 2013 Bunched Above in 2013Note: This figure plots the distribution of taxable income in year t for firms that bunched in year t− 1.134C.2 The composition of bunchersWe might expect tax collectors to assign higher prepayments, and to limit access to preferentialrates, to firms they perceive to be ineligible or more able to pay higher tax burdens. The structure oftax administration in China makes this quite plausible. Local tax collectors are typically responsiblefor a portfolio of local taxpayers. They interact locally, and frequently, allowing tax collectors toaccumulate informal first-hand knowledge of firms under their purview. It is not implausible thattax collectors come to use this informal, in-person, knowledge when exercising their discretion overthe firm’s deemed eligibility for tax policies.As an indirect test of this, we examine whether firms that bunch-above are systematicallydifferent than those that bunch-below. To do so, for each threshold Tt in effect in year t we define anarrow bandwidth bT,t of taxable income around this threshold. We restrict the sample to firms withreported taxable income yit in bandwidth bT,t. For firm i, in region r, in time t, within bandwidthbT,t around threshold Tt, we assign them an indicator 1i,t,r if they are below the threshold, and zeroif they are above. We then estimate a logistic regression with an underlying latent function of theform:1i,t,r = Xi,tβx +∑bT,tγb1yi,t∈bT,t +2015∑s=2010γs × 1t=s +∑hγh × 1r=h + εit (C.1)Where γs are year fixed effects, γh tax bureau fixed effects, and γb are threshold fixed effects.The coefficients αh and αl represent fixed effects for being in the lowest prepayment group andthe highest prepayment group respectively. The base group are firms with prepayments in themiddle prepayment region. We include a range of firm characteristics in Xi,t. We care about whichtypes of firms are more likely to bunch-above versus bunch-below. Table C.1 reports the averagemarginal effects for each variable. Columns (1) and (2) show the coefficients and standard errors ofthe baseline in equation (C.1) without tax bureau fixed effects, while columns (3) and (4) show theresults including them. We restrict to observations from 2010 to 2013 to focus on the pre-reformperiod and to firms that are eligible according to the asset cutoffs.First we focus on measures of firm size often readily observable to tax collectors: the stockof fixed assets and the number of employees. As shown in Table C.1, firms with larger fixedassets stocks are less likely to bunch below the threshold. A 10 percent increase in the asset stockcorrelates with .7 percentage point reduction in the likelihood of bunching below the notch. This isconsistent with the notion that tax collectors are more likely to deny eligibility to firms they deeminherently less eligible for small-business tax breaks. We find not evidence of a similar effect fromthe number of employees. This is not surprising as our measure of employees is reported only fora single period and therefore contains substantial measurement error.135Table C.1: Predictors of bunching-below vs. -above (pre-reform)Coef Std. Error Coef Std. ErrorAge -0.001 (0.001) -0.001 (0.001)Prepayments ≤ Lower Threshold 0.453*** (0.011) 0.462*** (0.010)Prepayments > Upper Threshold -0.065*** (0.015) -0.077*** (0.015)Log (Assets) -0.007* (0.003) -0.007* (0.003)Log (Employees ) -0.006 (0.005) -0.008 (0.005)State and collectively-owned -0.001 (0.008) -0.002 (0.008)Other Ownership Form -0.003 (0.057) 0.011 (0.061)Agriculture, forestry, fisheries 0.255** (0.087) 0.252** (0.082)Construction 0.051*** (0.015) 0.045** (0.015)Culture, sports, entertainment 0.049 (0.076) 0.040 (0.071)Education 0.032 (0.039) 0.026 (0.041)Energy and utilities -0.056 (0.045) -0.051 (0.043)Financial services -0.204 (0.143) -0.250 (0.132)Health and social work 0.057 (0.085) 0.055 (0.091)Hydrolics, environment and other 0.003 (0.064) 0.016 (0.060)Lodging and food services 0.044* (0.020) 0.047* (0.019)Mining 0.327*** (0.014) 0.313*** (0.050)Real estate 0.010 (0.029) -0.003 (0.030)Rental and business services 0.035 (0.026) 0.027 (0.026)Residential services 0.021 (0.026) 0.021 (0.025)S. Public administration, social -0.091 (0.158) -0.128 (0.165)Science, research, technology 0.032 (0.039) 0.014 (0.034)Telecommunication, software, IT 0.081*** (0.023) 0.068** (0.025)Transportation and logistics 0.054*** (0.013) 0.046** (0.014)Wholesale and retail 0.021 (0.012) 0.015 (0.013)N 14411 14411R2 0.25 0.28Tax Bureau Fixed Effects No YesYear Fixed Effects Yes YesNotch Fixed Effects Yes YesNote: This figure shows the point estimates from estimating equation (C.1). The sampleis restricted to firms with taxable income within a 5 percent bandwidth around thenotches in the given year – each year has two notes: the micro enterprise threshold andthe small enterprise threshold. The outcome variable is 1 if the firm has taxable incomebelow the notch, and 0 if above. The regression includes industry and ownership-formfixed effects. The ommitted base group for each are Manufacturing and Privately-Ownedrespectively. Standard errors are clustered at the four digit industry level.136C.3 2014 Policy directiveThe following are the relevant excerpts from the policy directive (bold added):The small low-profit enterprises that meet the prescribed conditions may, in the pro-cess of prepayment and annual final settlement and payment of enterprise income tax,enjoy at their own discretion the preferential policies of enterprise incometax applicable to small low-profit enterprises without the examination andapproval of tax authorities, but shall, when submitting annual enterprise incometax returns, concurrently report the information on the employees and total assets ofenterprises to tax authorities for recordation [...] the previous administrative provisionsshall be reviewed and the approval requirements issued by all localities shallbe canceled according to the provision that the small low-profit enterpriseswhich enjoy preferential policies shall be changed to be subject to recorda-tion administration. Henceforth, the tax authorities at all levels shall neitheralter or set the management mode without permission for any reason norconduct approval in disguised form. Third, the acceptance of materials shall beregulated according to unified requirements, and no small low-profit enterprise shall berequired to submit additional statements or materials.The tax authorities at all levels shall, according to the characteristics of small low-profitenterprises, strengthen policy publicity, conduct publicity and media cover-age through multiple channels and platforms from various perspectives, andincorporate the publicity and implementation activities into the unified deployment ofthe Spring Breeze Campaign to Facilitate Citizens’ Handling of Tax Affairs of tax au-thorities; and shall make full use of radio, television, Internet, SMS and 12366hotline to extensively publicize the content of the preferential income taxpolicies for small low-profit enterprises, and the procedures for handling taxaffairs, declaration requirements and management models thereof, especiallythat the small low-profit enterprises subject to verified tax collection are allowed toenjoy the preferential policies, among others, so as to make these policies known to thegeneral public.The tax authorities at all levels shall, in consideration of the adjustments to the man-agement mode for the enjoyment of preferential policies by small low-profit enterprises,take effective measures to improve the follow-up management. First, in the process ofor after final settlement and payment, the information on the enjoyment of preferentialpolicies by small low-profit enterprises shall be obtained in a timely manner. For smalllow-profit enterprises which have not enjoyed the policy on half-reduced enterprise in-137come tax, the formalities for tax refund or for tax deduction from the taxamount payable in the following year shall be handled in a timely manner.138Figure C.2: Prepayment Descriptives(a) Prepayment Density0.05.1.15.2Kdensity0 .2 .4 .6 .8 1 1.2 1.4 1.6Prepayment RatioFirm-Years With Taxable Income Less than 100,000Firm-Years with Taxable Income between 400,000 and 1,000,000Firm-Years with Taxable Income Greater than 1,000,000(b) Average and Median Prepayment Ratios.6.811.2Average Prepayment Ratio14 16 18 20 22 24Log of Taxable IncomeAverage Prepayment RatioMedian Prepayment RatioNote: Panel A estimates a kernel density of the prepayment ratio, defined as the percent of the year-end tax liabilitythat was paid in advance, separately for firms with taxable income less than 100,000, firms with taxable incomebetween 400,000 and 1,000,000, and firms with taxable income larger than 1,000,000. The vertical black line at .7represemts an internal lower-bound target among tax collectors. Panel B plots the average and median ratio amongincome bins (in logs). The average prepayment ratio hovers around 80 percent across the firm size distribution, andthe median between 90 and 100 percent.139Figure C.3: Composition of bunchers by prepayment region(a) 2010-20110.2.4.6PercentWrong-Side Bunchers Correct-Side BunchersLower RegionAmbiguous RegionUpper RegionLower RegionAmbiguous RegionUpper Region(b) 2012-20130.2.4.6PercentWrong-Side Bunchers Correct-Side BunchersLower RegionAmbiguous RegionUpper RegionLower RegionAmbiguous RegionUpper Region(c) 20140.2.4.6.8PercentWrong-Side Bunchers Correct-Side BunchersLower RegionAmbiguous RegionUpper RegionLower RegionAmbiguous RegionUpper Region(d) 2015 Eligible0.2.4.6.8PercentWrong-Side Bunchers Correct-Side BunchersLower RegionAmbiguous RegionUpper RegionLower RegionAmbiguous RegionUpper RegionNote: This figure visualizes the composition of bunchers. For a given notch, we restrict the sample to firms with taxable income within a 5 percent windowaround the notch. These are the “bunchers”. Wrong-side bunchers are firms with taxable income above the notch. Correct-side bunchers are firms withtaxable income below the notch. For each group, we plot the percent of firms in each of the three implicit prepayment regions. Wrong-side bunchersdisporportionately fall within the ambiguous prepayment region. Alternatively, correct-side bunchers are much more likely to have prepayments in thelower prepayment regions.140Figure C.4: Prepayment behavior over time: Micro-enterprise thresholds(a) 2010-20110.02.04.06Frequency0 2000 4000 6000 8000 10000Prepayment(b) 2012-2013.01.02.03.04Frequency4000 6000 8000 10000 12000 14000PrepaymentEligible Ineligible(c) 20140.01.02.03.04Frequency5000 10000 15000 20000 25000PrepaymentEligible Ineligible(d) 20150.01.02.03.04Frequency10000 20000 30000 40000 50000PrepaymentEligible Ineligible(e) 20160.01.02.03.04Fequency20000 30000 40000 50000 60000 70000 80000PrepaymentEligible IneligibleNote: This figure bins firms into equal-width bins based on prepayments. For each prepayment bin, the frequencyof firms is plotted. The markers represent the right-hand endpoints (inclusive). The plots show the distributionsfor both eligible and ineligible firms, where eligibility is determined according to the asset threshold. In practice,firms’s employee counts must also be below a threshold, but we do not observe employee counts. We are unable todetermine eligibility in 2010/2011 due to an absence of asset information. The the distribution in Panel A representsboth groups of firms.141Figure C.5: Prepayment behavior over time: Small-enterprise thresholds(a) 20120.01.02.03.04Frequency40000 50000 60000 70000 80000 90000PrepaymentEligible Ineligible(b) 20130.01.02.03.04Frequency40000 50000 60000 70000 80000 90000PrepaymentEligible Ineligible(c) 20140.01.02.03.04Frequency40000 50000 60000 70000 80000 90000PrepaymentEligible Ineligible(d) 20150.01.02.03.04Frequency40000 50000 60000 70000 80000 90000PrepaymentEligible IneligibleNote: This figure bins firms into equal-width bins based on prepayments. For each prepayment bin, the frequencyof firms is plotted. The markers represent the right-hand endpoints (inclusive). The plots show the distributions forboth eligible and ineligible firms, where eligibility is determined according to the asset threshold. In practice, firms’semployee counts must also be below a threshold, but we do not observe employee counts. We are unable to determineeligibility in 2010/2011 due to an absence of asset information. The the distribution in Panel A represents both groupsof firms for this reason. In 2015, the tax authority announced that the micro-enterprie threshold would be increasedfrom 200,000 to 300,000, effectively combining the small and micro thresholds. Taxable income corresponding tothe last quarter of 2015 was eligible to receive the preferential rate of 10 percent. Thereby, a firm with final taxableincome between 200,000 and 300,000 would pay face a 17.5 percent tax rate, rather than 20 percent. The third dottedline in Panel D represents the corresponding implicit prepayment threshold.142Figure C.6: Number of refunds granted010000200003000040000Frequency2010m1 2012m1 2014m1 2016m1Note: This figure plots the number of income tax refunds granted per month. The vertical red line marks the policydirective implemented in July, 2014. The spike occured in the week of September 17-21, 2014.143

Cite

Citation Scheme:

        

Citations by CSL (citeproc-js)

Usage Statistics

Share

Embed

Customize your widget with the following options, then copy and paste the code below into the HTML of your page to embed this item in your website.
                        
                            <div id="ubcOpenCollectionsWidgetDisplay">
                            <script id="ubcOpenCollectionsWidget"
                            src="{[{embed.src}]}"
                            data-item="{[{embed.item}]}"
                            data-collection="{[{embed.collection}]}"
                            data-metadata="{[{embed.showMetadata}]}"
                            data-width="{[{embed.width}]}"
                            data-media="{[{embed.selectedMedia}]}"
                            async >
                            </script>
                            </div>
                        
                    
IIIF logo Our image viewer uses the IIIF 2.0 standard. To load this item in other compatible viewers, use this url:
https://iiif.library.ubc.ca/presentation/dsp.24.1-0395341/manifest

Comment

Related Items