THE COMPLEXITIES OF PUBLIC GOODS FOR A 
DIVERSE PUBLIC: EVIDENCE FROM GUN LAWS, 
CLIMATE POLICY, AND POLICE TRANSPARENCY
by
GARRETT OLSON STANFORD
A DISSERTATION
Presented to the Department of Economics
and the Division of Graduate Studies of the University of Oregon
in partial fulfillment of the requirements
for the degree of
Doctor of Philosophy
June 2023
DISSERTATION APPROVAL PAGE
Student: Garrett Olson Stanford
Title: The Complexities of Public Goods for a Diverse Public:
Evidence from Gun Laws, Climate Policy, and Police Transparency
This dissertation has been accepted and approved in partial fulfillment of the requirements
for the Doctor of Philosophy degree in the Department of Economics by:
Edward Rubin Chair
Trudy Ann Cameron Core Member
Jonathan M. Davis Core Member
Bryce Newell Institutional Representative
and
Krista Chronister Vice Provost for Graduate Studies
Original approval signatures are on file with the University of Oregon Division of
Graduate Studies.
Degree awarded June 2023
ii
© 2023 Garrett Olson Stanford
This work is licensed under a Creative Commons
Attribution-NonCommercial (United States) License.
iii
DISSERTATION ABSTRACT
Garrett Olson Stanford
Doctor of Philosophy
Department of Economics
June 2023
Title: The Complexities of Public Goods for a Diverse Public:
Evidence from Gun Laws, Climate Policy, and Police Transparency
This research examines three pressing social issues: tensions between law
enforcement and the public, climate change policy options, and firearms control laws.
Chapter 2 and Chapter 3 use field and survey-based experiments to collect primary data.
They estimate novel measures, respectively, of police behavior and public preferences
concerning climate change policy. Chapter 4 uses newly available administrative data to
understand the consequences of a recently passed firearms control law.
In Chapter 2, I test for evidence of racial and gender biases in one aspect of police
interactions with the public in the United States. Using a so-called “correspondence”
study, I test whether police departments respond differently to requests for information
about how to lodge a formal complaint against an officer in the department depending
on the perceived race/ethnicity and gender of the complainant. The study’s experimental
design allows me to examine police behavior quantitatively without relying on police-
provided administrative data. Results for a nationwide random sample of police
departments suggest that police departments are less likely to respond to Black and
Hispanic individuals than White individuals. Examining the interaction of race/ethnicity
and gender, I find police departments are most likely to respond to White males and least
likely to respond to Black and Hispanic males.
iv
Chapter 3 reports upon the results from a set of survey-based choice experiments
designed to assess state-level demand for carbon cap-and-trade programs with different
attributes. The evidence confirms that these state-level preferences are strongly
heterogeneous with respect to political ideologies and opinions about climate change. Our
models allow us to calculate the implied social benefits of carbon emissions reductions.
We estimate the marginal rate of substitution between “carbon” jobs and “green” jobs for
different preference classes. We then use our estimates to model how support for different
types of cap-and-trade programs varies across the United States. Methodologically, we
account for systematic sample selection of respondents in our estimating sample relative
to the quota-based sample of invitees from our commercial internet panel.
In Chapter 4, we examine the (un)intended effects of Oregon’s new firearms
control law: Measure 114. Narrowly passing by a popular referendum vote in November
2022, Measure 114 aimed to increase firearms licensing requirements and restrict access
to high-capacity magazines for ammunitions. We use data from the FBI’s National
Instant Criminal Background Check System and an administrative dataset provided
by the Oregon State Police to measure the causal effect of the law on firearm sales.
Results indicate that Measure 114 unintentionally motivated Oregonians to purchase an
unprecedented increase in the number of firearms.
This dissertation includes previously unpublished co-authored material.
v
CURRICULUM VITAE
NAME OF AUTHOR: Garrett Olson Stanford
GRADUATE AND UNDERGRADUATE SCHOOLS ATTENDED:
University of Oregon, Eugene, OR
Portland State University, Portland, OR
Kanda Institute of International Studies, Chiba, Japan
University of Puget Sound, Tacoma, OR
DEGREES AWARDED:
Doctor of Philosophy, Economics, 2023, University of Oregon
Master of Science, Economics, 2019, University of Oregon
Bachelor of Science, Economics, 2014, University of Puget Sound
Bachelor of Arts, Japanese, 2014, University of Puget Sound
AREAS OF SPECIAL INTEREST:
Public economics
Experimental economics
Environmental economics
Criminal Justice
vi
ACKNOWLEDGEMENTS
I thank Professors Edward Rubin, Trudy Ann Cameron, Jonathan Davis, and
Bryce Newell for their advice, mentorship, and unwavering support. I am incredibly
grateful to Professor Rubin for his kindness and ability to keep me positive in the most
daunting of times and to Professor Cameron for being the most supportive and selfless
mentor for whom anyone could ever ask. I also thank Professor Ben Hansen for his
helpful insights and much-needed support in the final stretch.
This research benefited from valuable comments from participants in the
University of Oregon Micro Group, the 2022 Society for Benefit-Cost Analysis Annual
Conference, the 2022 AERE Summer Conference, and the 2022 WEAI Conference.
I wish to thank my fellow University of Oregon Economics graduate students, for,
among many things, their camaraderie. I especially want to thank Robert McDonough,
Promise Kamanga, Tanner Bivins, and John Morehouse. Without them, this dissertation
would be an abandoned dream.
Finally, I thank my friends and family who supported me throughout this
endeavor. In particular, my sister Lydia, for being a good listener, a generous soul,
and an excellent ear to gripe to; Lucas for his selfless acts of service; and my steadfast
rock throughout this all: Claire, I could not be more grateful for your love, support, and
exquisite sense of humor <3
This work has been supported in part by the endowment accompanying the
Raymond F. Mikesell Chair in Environmental and Resource Economics at the University
of Oregon. Any remaining errors are my own.
vii
To Tom, for being alive for so long; good job!
viii
TABLE OF CONTENTS
Chapter Page
I. INTRODUCTION . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1
II. POLICE ARE LESS LIKELY TO
RESPOND TO REQUESTS FOR HELP FROM MINORITIES:
FIELD EXPERIMENT EVIDENCE OF POLICE
DISCRIMINATION . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4
2.1. Overview . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5
2.2. Experimental Design and Data . . . . . . . . . . . . . . . . . . . . . . 12
2.2.1. Experiment . . . . . . . . . . . . . . . . . . . . . . . . . . . 12
2.2.2. Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16
2.3. Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18
2.3.1. Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . 18
2.3.2. Main results . . . . . . . . . . . . . . . . . . . . . . . . . . . 19
2.3.2.1. Interaction Effects . . . . . . . . . . . . . . . . . . . 21
2.3.2.2. Department Size . . . . . . . . . . . . . . . . . . . 24
2.4. Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 25
2.4.1. Interpreting Bias . . . . . . . . . . . . . . . . . . . . . . . . 25
2.4.2. Accountability . . . . . . . . . . . . . . . . . . . . . . . . . 27
2.4.3. Caveats . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28
2.4.4. Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . 30
2.5. Tables Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 31
III. PUBLIC PREFERENCES FOR A STATE-LEVEL CARBON
CAP-AND-TRADE PROGRAM . . . . . . . . . . . . . . . . . . . . . . 42
3.1. Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 43
3.2. Basic Choice Model . . . . . . . . . . . . . . . . . . . . . . . . . . . 48
ix
Chapter Page
3.2.1. Homogeneous preferences . . . . . . . . . . . . . . . . . . . . 48
3.2.2. Heterogeneous preferences . . . . . . . . . . . . . . . . . . . 54
3.2.2.1. Mixed logit models . . . . . . . . . . . . . . . . . . 54
3.2.2.2. Latent class models . . . . . . . . . . . . . . . . . . 57
3.2.2.3. Preferences that vary systematically with
observable respondent characteristics . . . . . . . . . 59
3.3. Outline of Survey and Data . . . . . . . . . . . . . . . . . . . . . . . 60
3.3.1. Sketch of the survey instrument . . . . . . . . . . . . . . . . . 60
3.3.2. Sample Selection . . . . . . . . . . . . . . . . . . . . . . . . 61
3.4. Results and Discussion . . . . . . . . . . . . . . . . . . . . . . . . . 63
3.4.1. Sample Selection . . . . . . . . . . . . . . . . . . . . . . . . 63
3.4.2. Program choice model: Homogeneous preferences . . . . . . . . 64
3.4.3. Program choices: Heterogeneous preferences . . . . . . . . . . 67
3.4.3.1. Unobserved heterogeneity: Mixed logit specifications . 67
3.4.3.2. Latent class models . . . . . . . . . . . . . . . . . . 68
3.4.4. Program choices: Observable heterogeneity and
benefits transfer . . . . . . . . . . . . . . . . . . . . . . . . . 71
3.4.5. Implications of estimated models . . . . . . . . . . . . . . . . 74
3.4.5.1. Benefit function transfer to all ZCTAs in
the lower-48 U.S. states . . . . . . . . . . . . . . . . 78
3.4.5.2. Distribution of WTP for cap-and-trade
programs across ZCTAs . . . . . . . . . . . . . . . . 79
3.4.5.3. Spatial heterogeneity in WTP for different
cap-and-trade programs . . . . . . . . . . . . . . . . 80
3.5. Directions for Future Research . . . . . . . . . . . . . . . . . . . . . 81
3.6. Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82
x
Chapter Page
IV. OREGUNIANS AND THE GUN-CONTROL PARADOX . . . . . . . . . 101
4.1. Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 102
4.2. Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 105
4.2.1. Gun laws in the United States . . . . . . . . . . . . . . . . . . 105
4.2.2. Gun laws in Oregon . . . . . . . . . . . . . . . . . . . . . . . 107
4.3. Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 108
4.4. Methodology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112
4.5. Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114
4.5.1. Treatment period . . . . . . . . . . . . . . . . . . . . . . . . 114
4.5.2. State-level synthetic control difference-in-difference . . . . . . . 115
4.5.3. Time-series models . . . . . . . . . . . . . . . . . . . . . . . 116
4.5.4. Event Study . . . . . . . . . . . . . . . . . . . . . . . . . . . 117
4.5.5. County Heterogeneity . . . . . . . . . . . . . . . . . . . . . . 118
4.6. Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 120
4.7. Tables and Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . 127
V. CONCLUSION . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 146
APPENDICES
A. CHAPTER 2 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . 148
A.1. Appendix: Police Department Selection . . . . . . . . . . . . . . . . . 148
A.1.1. Type of email collected . . . . . . . . . . . . . . . . . . . . . 149
A.2. Appendix: Identity Construction . . . . . . . . . . . . . . . . . . . . . 151
A.3. Appendix: Email Account Creation . . . . . . . . . . . . . . . . . . . 155
A.4. Appendix: Example Email . . . . . . . . . . . . . . . . . . . . . . . 156
A.4.1. Email Text . . . . . . . . . . . . . . . . . . . . . . . . . . . 156
A.5. Appendix: Treatment Assignment . . . . . . . . . . . . . . . . . . . . 158
xi
Chapter Page
A.6. Appendix: Experiment Implementation . . . . . . . . . . . . . . . . . 163
A.7. Appendix: Response Time and Word Count . . . . . . . . . . . . . . . 165
A.8. Appendix: Summary Statistics . . . . . . . . . . . . . . . . . . . . . . 168
B. CHAPTER 3 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . 173
B.1. Appendix: Expanded Discussion of the Related Literature . . . . . . . . 174
B.1.1. Context . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 174
B.1.2. Cap-and-Trade Attributes . . . . . . . . . . . . . . . . . . . . 174
B.1.2.1. Jobs . . . . . . . . . . . . . . . . . . . . . . . . . . 175
B.1.2.2. Costs . . . . . . . . . . . . . . . . . . . . . . . . . 176
B.1.2.3. Permit Allocation . . . . . . . . . . . . . . . . . . . 177
B.1.2.4. Permit auction revenue use . . . . . . . . . . . . . . 177
B.1.2.5. Additional Regulations . . . . . . . . . . . . . . . . 178
B.1.3. Political Obstacles . . . . . . . . . . . . . . . . . . . . . . . . 179
B.2. Appendix: Structure of the Survey . . . . . . . . . . . . . . . . . . . . 181
B.2.1. Demographic Questions for Screening . . . . . . . . . . . . . . 181
B.2.2. Intro Questions . . . . . . . . . . . . . . . . . . . . . . . . . 182
B.2.3. Background Information . . . . . . . . . . . . . . . . . . . . . 182
B.2.4. Tutorial on Program Attributes . . . . . . . . . . . . . . . . . 183
B.2.5. Choice Scenarios . . . . . . . . . . . . . . . . . . . . . . . . 187
B.2.6. Follow-up Questions . . . . . . . . . . . . . . . . . . . . . . 190
B.3. Appendix: One Instance of the Survey (Screenshots) . . . . . . . . . . . 197
B.3.1. State of residence . . . . . . . . . . . . . . . . . . . . . . . . 197
B.3.2. Age . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 198
B.3.3. Gender . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 198
B.3.4. Race . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 199
xii
Chapter Page
B.3.5. Household income . . . . . . . . . . . . . . . . . . . . . . . 199
B.3.6. ZIP code . . . . . . . . . . . . . . . . . . . . . . . . . . . . 200
B.3.7. Check ZIP code . . . . . . . . . . . . . . . . . . . . . . . . . 201
B.3.8. Confirm standard ZIP code . . . . . . . . . . . . . . . . . . . 201
B.3.9. Consent to Participate . . . . . . . . . . . . . . . . . . . . . . 201
B.3.10. Oath . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 202
B.3.11. Introduction to climate change . . . . . . . . . . . . . . . . . . 202
B.3.12. Introduction to carbon emissions . . . . . . . . . . . . . . . . . 203
B.3.13. Introduction to controversy of cap-and-trade in Oregon . . . . . 204
B.3.14. Introduction to cap-and-trade programs . . . . . . . . . . . . . 205
B.3.15. Introduction to program coverage . . . . . . . . . . . . . . . . 206
B.3.16. Introduction to program coverage, continued . . . . . . . . . . . 207
B.3.17. Introduction to permit auctions . . . . . . . . . . . . . . . . . 207
B.3.18. Introduction to grandfathering process . . . . . . . . . . . . . . 208
B.3.19. Introduction to revenue distribution . . . . . . . . . . . . . . . 209
B.3.20. Introduction to benefits of carbon emissions reductions . . . . . . 209
B.3.21. Introduction to possible distributional concerns . . . . . . . . . 211
B.3.22. Oregon county of residence . . . . . . . . . . . . . . . . . . . 212
B.3.23. Confirm county of residence . . . . . . . . . . . . . . . . . . . 212
B.3.24. Introduce program summary tables . . . . . . . . . . . . . . . 213
B.3.25. Explain Feature Group 1 . . . . . . . . . . . . . . . . . . . . . 213
B.3.26. Explain Feature Group 2 . . . . . . . . . . . . . . . . . . . . . 216
B.3.27. Explain Feature Group 3 . . . . . . . . . . . . . . . . . . . . . 217
B.3.28. Explain Feature Group 4 . . . . . . . . . . . . . . . . . . . . . 218
B.3.29. Explain Feature Group 5 . . . . . . . . . . . . . . . . . . . . . 219
xiii
Chapter Page
B.3.30. Program A choice . . . . . . . . . . . . . . . . . . . . . . . . 221
B.3.31. Follow-up to “No” vote: Reasons for vote . . . . . . . . . . . . 222
B.3.32. Follow-up to “No” vote: Will you always vote no? . . . . . . . . 223
B.3.33. Program B choice . . . . . . . . . . . . . . . . . . . . . . . . 224
B.3.34. Program C choice . . . . . . . . . . . . . . . . . . . . . . . . 225
B.3.35. Program D choice . . . . . . . . . . . . . . . . . . . . . . . . 226
B.3.36. Program E choice . . . . . . . . . . . . . . . . . . . . . . . . 227
B.3.37. Program F choice . . . . . . . . . . . . . . . . . . . . . . . . 228
B.3.38. Follow-up to “No” vote . . . . . . . . . . . . . . . . . . . . . 229
B.3.39. Preferences for policies other than cap-and-trade . . . . . . . . . 229
B.3.40. Most important attributes . . . . . . . . . . . . . . . . . . . . 230
B.3.41. Attachment to Oregon . . . . . . . . . . . . . . . . . . . . . . 230
B.3.42. Ethnicity . . . . . . . . . . . . . . . . . . . . . . . . . . . . 231
B.3.43. Sectors providing household income . . . . . . . . . . . . . . . 231
B.3.44. Political ideology . . . . . . . . . . . . . . . . . . . . . . . . 232
B.3.45. Political party identification . . . . . . . . . . . . . . . . . . . 233
B.3.46. Educational Attainment . . . . . . . . . . . . . . . . . . . . . 233
B.3.47. Employment status . . . . . . . . . . . . . . . . . . . . . . . 233
B.3.48. Attitude: climate change real and serious . . . . . . . . . . . . 234
B.3.49. Attitude: climate change human-caused . . . . . . . . . . . . . 234
B.3.50. Attitude: responsibility to fix climate . . . . . . . . . . . . . . 235
B.3.51. Inter-generational concern: descendants . . . . . . . . . . . . . 235
B.3.52. Inter-generational concern: ancestors . . . . . . . . . . . . . . 235
B.3.53. Primary heating fuel used . . . . . . . . . . . . . . . . . . . . 236
B.3.54. Usual forms of transportation . . . . . . . . . . . . . . . . . . 236
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Chapter Page
B.3.55. Perception of researcher bias . . . . . . . . . . . . . . . . . . 237
B.3.56. Attitude: Respondent’s experience with survey . . . . . . . . . . 237
B.3.57. Feedback text message . . . . . . . . . . . . . . . . . . . . . 238
B.4. Appendix: Selection Model and Selection Correction . . . . . . . . . . 239
B.4.1. Variable Selection . . . . . . . . . . . . . . . . . . . . . . . . 239
B.4.1.1. Inventory of candidate explanatory variables . . . . . . 239
B.4.1.2. Probit selection model . . . . . . . . . . . . . . . . . 242
B.4.2. Selection Correction Strategy . . . . . . . . . . . . . . . . . . 243
B.5. Appendix: Choice Experiment Randomizations . . . . . . . . . . . . . 247
B.6. Appendix: Descriptive Statistics for Some Basic Variable Relationships . 253
B.6.1. Relationships among respondent characteristics and attitudes . . . 253
B.6.2. Share of "YES" votes for program by category of respondent . . . 253
B.6.3. Share of "YES" votes by aspect of choice task . . . . . . . . . . 264
B.6.4. Identical distributions of program attributes across tasks? . . . . 269
B.6.5. Votes as a function of non-mutually exclusive categories . . . . . 274
C. CHAPTER 4 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . 277
C.1. Online Appendix: Sensitivity Analysis . . . . . . . . . . . . . . . . . . 277
REFERENCES CITED . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 279
xv
LIST OF FIGURES
Figure Page
1. Department Selection Heat Map . . . . . . . . . . . . . . . . . . . . . . . 40
2. Response time summary . . . . . . . . . . . . . . . . . . . . . . . . . . 41
3. Distribution of predicted WTP for basic cap-and-trade program . . . . . . . 87
4. Distribution of predicted WTP for alternative cap-and-trade program . . . . . 88
5. Map of predicted WTP for basic cap-and-trade program . . . . . . . . . . . 89
6. Map of predicted WTP for alternative basic cap-and-trade program . . . . . 90
7. FBI vs. OSP data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134
8. Google Trends search for Measure 114 . . . . . . . . . . . . . . . . . . . 135
9. Synthetic control difference-in-difference for Oregon
background checks (per capita) . . . . . . . . . . . . . . . . . . . . . . . 136
10. Weekly timeseries (2018-2022) . . . . . . . . . . . . . . . . . . . . . . . 137
11. Weekly timeseries (2022) . . . . . . . . . . . . . . . . . . . . . . . . . . 138
12. Daily timeseries . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 139
13. Event Study for OSP background checks (11-08) . . . . . . . . . . . . . . 140
14. Event Study for OSP background checks (10-2) . . . . . . . . . . . . . . . 141
15. Timeseries for by majority vote share (2018-2022) . . . . . . . . . . . . . . 142
16. Timeseries by majority vote share (2022) . . . . . . . . . . . . . . . . . . 143
17. Timeseries by quartile vote share (2018-2022) . . . . . . . . . . . . . . . . 144
18. Timeseries by quartile vote share (2022) . . . . . . . . . . . . . . . . . . . 145
B1. Example email . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 157
B2. Example email . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 157
B3. Emails sent by week. . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161
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Figure Page
B4. Departments by state included in the study. . . . . . . . . . . . . . . . . . 162
B5. Mean response rate by week by identities . . . . . . . . . . . . . . . . . . 168
B6. Mean response rate by week for all putative identities . . . . . . . . . . . . 169
B7. Response rates differentials by local population size . . . . . . . . . . . . . 170
B8. Response rates differentials by local department size . . . . . . . . . . . . . 172
D1. Demeaned response propensities . . . . . . . . . . . . . . . . . . . . . . 246
E1. Distribution of job loss randomizations . . . . . . . . . . . . . . . . . . . 249
E2. Distribution of program cost randomizations . . . . . . . . . . . . . . . . . 252
F1. Descriptive Statistics: Bias by ideology . . . . . . . . . . . . . . . . . . . 253
F2. Descriptive Statistics: Votes by age . . . . . . . . . . . . . . . . . . . . . 254
F3. Descriptive Statistics: Votes by income . . . . . . . . . . . . . . . . . . . 255
F4. Descriptive Statistics: Votes by ideology . . . . . . . . . . . . . . . . . . . 256
F5. Descriptive Statistics: Votes by education . . . . . . . . . . . . . . . . . . 257
F6. Descriptive Statistics: Votes by employment . . . . . . . . . . . . . . . . . 258
F7. Descriptive Statistics: Votes by climate 1 . . . . . . . . . . . . . . . . . . 259
F8. Descriptive Statistics: Votes by climate 2 . . . . . . . . . . . . . . . . . . 260
F9. Descriptive Statistics: Votes by ancestors . . . . . . . . . . . . . . . . . . 261
F10. Descriptive Statistics: Votes by cost decile . . . . . . . . . . . . . . . . . . 262
F11. Descriptive Statistics: Votes by benefits . . . . . . . . . . . . . . . . . . . 263
F12. Descriptive Statistics: Votes by task . . . . . . . . . . . . . . . . . . . . . 265
F13. Descriptive Statistics: Party votes by task . . . . . . . . . . . . . . . . . . 266
F14. Descriptive Statistics: Time on task . . . . . . . . . . . . . . . . . . . . . 267
F15. Descriptive Statistics: Touches per task . . . . . . . . . . . . . . . . . . . 267
F16. Descriptive Statistics: Clicks per task . . . . . . . . . . . . . . . . . . . . 268
F17. Descriptive Statistics: Cost per task . . . . . . . . . . . . . . . . . . . . . 269
xvii
Figure Page
F18. Descriptive Statistics: Benefits per task . . . . . . . . . . . . . . . . . . . 270
F19. Descriptive Statistics: Carbon jobs per task . . . . . . . . . . . . . . . . . 270
F20. Descriptive Statistics: Green jobs per task . . . . . . . . . . . . . . . . . . 271
F21. Descriptive Statistics: Auction per task . . . . . . . . . . . . . . . . . . . 271
F22. Descriptive Statistics: Equipment per task . . . . . . . . . . . . . . . . . . 272
F23. Descriptive Statistics: Workers per task . . . . . . . . . . . . . . . . . . . 272
F24. Descriptive Statistics: Relief per task . . . . . . . . . . . . . . . . . . . . 273
F25. Descriptive Statistics: Regulations per task . . . . . . . . . . . . . . . . . 273
F26. Descriptive Statistics: Votes by sector . . . . . . . . . . . . . . . . . . . . 274
F27. Descriptive Statistics: Votes by responsibility . . . . . . . . . . . . . . . . 275
F28. Descriptive Statistics: Votes by descendants . . . . . . . . . . . . . . . . . 275
F29. Descriptive Statistics: Votes by transportation . . . . . . . . . . . . . . . . 276
A1. Synthetic control difference-in-difference for Oregon
background checks (raw count) . . . . . . . . . . . . . . . . . . . . . . . 278
xviii
LIST OF TABLES
Table Page
1. Comparison of departments included and excluded from experiment . . . . . 32
2. Identity Creation: Last names used in study . . . . . . . . . . . . . . . . . 33
3. Identity Creation: First names used in study . . . . . . . . . . . . . . . . . 34
4. Balance Table . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35
5. Emails Categorized by Outcome . . . . . . . . . . . . . . . . . . . . . . . 36
6. Response Rate Differences by Race and Gender . . . . . . . . . . . . . . . 37
7. Response Rate Differences for Race and Gender Interactions . . . . . . . . . 38
8. Department Size Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . 39
9. Descriptive statistics for cap-and-trade programs and for
alternative ways of capturing individual preference heterogeneity . . . . . . . 91
10. Descriptive statistics for ZCTA-level heterogeneity in
preferences selected by LASSO for Model 5 . . . . . . . . . . . . . . . . . 92
11. Differences in baseline marginal utility parameter estimates
across alternative specifications . . . . . . . . . . . . . . . . . . . . . . . 94
12. Additional parameters for Model (2) in Table 11 . . . . . . . . . . . . . . . 96
13. Additional parameters for Model (3) in Table 11 . . . . . . . . . . . . . . . 96
14. Additional parameters for Model (4) in Table 11 . . . . . . . . . . . . . . . 97
15. Additional parameters for Model 5 in Table 11 . . . . . . . . . . . . . . . . 98
16. For comparison, different implications of estimated utility
parameters across specifications . . . . . . . . . . . . . . . . . . . . . . . 100
17. Firearm laws in 2023 . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128
18. Change in Oregon Background Checks after Measure 114 . . . . . . . . . . 131
19. Cummulative change in Oregon Background Checks after
Measure 114 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
xix
Table Page
20. County-level changes in Oregon Background Checks after
Measure 114 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133
B1. Distribution of Race, Ethnicity and Gender identity assignment
by state . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 160
B2. Distribution of Race, Ethnicity and Gender identity assignment
by week . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 163
B3. Response time and word count of response measured across identities . . . . 166
D1. Descriptive statistics: response/non-response models) . . . . . . . . . . . . 241
D2. Binary probit parameter estimates for selection model . . . . . . . . . . . . 245
xx
CHAPTER I
INTRODUCTION
Economics as a discipline has expanded its scope of study immensely over the last
few decades. This is due, in part, to the explosion of Big Data and Data Science methods,
in tandem with advancements in computing technology. These two developments have
opened doors to styles and topics of research previously considered infeasible, redefining
what economists can study. The growing breadth of topics might also be attributed to
shifting attitudes about what economists should study. These changing attitudes are
driven by a combination of two prevailing forces. First, economists are realizing the
potential benefits of using the tools and methods of economics to complement work
done by researchers in other social science fields. Second, the global community is faced
with an onslaught of pressing, complex and incredibly challenging social issues. Coping
with these challenges and designing effective policy responses for any of these social
crises requires a cross-disciplinary approach. The following chapters pertain to three of
the many crises of our time: interactions between police and the public, market-based
policies to limit climate change, and the (un)intended effects of firearms control laws.
This dissertation highlights topics that economists can address quantitatively and where
an economic perspective can help governments design better policies.
Chapter 2 contributes to a growing literature that checks for evidence of bias
in policing in the United States. I use an experimentally designed correspondence
study to test statistically whether police departments respond differently to requests for
information based on the perceived race/ethnicity or gender of the requester. I send email
requests to more than 2,000 U.S. police departments asking for information about how
to lodge a formal complaint about an officer in that department. I systematically vary
the putative race/ethnicity (Black, Hispanic and White) and gender (male and female) of
1
the email sender. I analyse response behavior on a handful of dimensions (e.g. whether
the department responds at all or how long it takes the department to respond). I then
examine which, if any, observable departmental or jurisdictional characteristics (e.g. size
of agency and median income for the department’s jurisdiction) are related systematically
to response behavior. One of the most valuable features of the the study’s design is that it
allows me to assess departments for evidence of police bias without relying on police-
provided data. Results indicate that police are statistically significantly less likely to
respond to requests from Black and Hispanic individuals than White individuals. In
addition, White males are the most likely to receive responses, while Black and Hispanic
males are the least likely.
Chapter 3 (co-authored with Trudy Ann Cameron) addresses the increasingly
pressing issue of climate change. The project was inspired by Oregon’s failed attempts
(in 2018 and 2020) to pass a state-wide carbon cap-and-trade program. Opponents of the
program advocated for a public referendum, but no referendum has taken place. In 2021,
we surveyed a representative sample of Oregonians about their preferences concerning a
range of hypothetical carbon cap-and-trade programs in Oregon. The survey is designed
so that we are able to estimate not only the total willingness to pay (WTP) values for
specific stylized programs, but also marginal willingness to pay for specific program
attributes. First, we estimate preference parameters and WTP values for a representative
Oregonian. Next, combining information volunteered by the respondents as well as a
publicly available geographic data (e.g., from the American Community Survey and
other geo-coded data), we estimate WTP values for different socio-demographic, regional
and ideological groups. Using our marginal WTP estimates, we can produce two novel
measures: (1) a social benefit of carbon (reduction) and (2) Oregonians’ marginal rate
of substitution between jobs in carbon-intensive industries and jobs in green industries.
2
Finally, we conduct a benefit function transfer exercise to illustrate the implications of our
estimates for support for carbon cap-and-trade programs at the ZCTA level across other
U.S. states.
Chapter 4 (co-authored with Katie Bollman, Ben Hansen, and Ed Rubin) examines
the impact of firearms control laws. As for Chapter 3, recent Oregon legislation inspired
this project. In November of 2022, Oregon voters narrowly passed Measure 114, an
initiative aimed to curb access to firearms and high-capacity magazines. In addition to
several other provisions, Measure 114 requires a permit to purchase a firearm for all
Oregonians. Consistent with literature that examines anticipatory firearm-purchasing
behavior, we document a surge in firearms sales in Oregon. In the first part of our
analysis, we use data at the state-month level on FBI background checks as a proxy
for firearms sales and apply a synthetic control difference-in-difference method to
establish a strong causal effect of Measure 114 on firearms sales in Oregon. We then
use background-check data provided by Oregon State Police to examine how Oregonians
have responded to Measure 114 at the daily and county level. Using time-series data and
event studies, we observe that Oregonians begin to increase their firearms purchases
ahead of election day in anticipation of the law. Furthermore, after the passage of
Measure 114 and before the law goes into effect, we observe a historic surge in firearms
sales—far outpacing the documented response to any other event in Oregon. The
observed stockpiling of firearms in response to Measure 114 is a critical lesson for
policymakers who may seek to curb the proliferation of firearms in the community. Akin
to the Green Paradox that exists in the world of environmental regulation, the anticipation
of restrictive laws can lead to unintended and counterproductive impacts. Addressing the
gun-related health crisis in the U.S. is essential for the welfare of American communities,
but policymakers should be wary of this “Steel Paradox.”
3
CHAPTER II
POLICE ARE LESS LIKELY TO RESPOND TO REQUESTS FOR HELP FROM
MINORITIES:
FIELD EXPERIMENT EVIDENCE OF POLICE DISCRIMINATION
Numerous high-profile incidents have led to accusations that police departments
struggle with equity and accountability. I use an experiment to test both. In the context
of a correspondence study, I send emails to more than 2,000 U.S. police departments
requesting information about how to lodge a complaint against an officer. Manipulating
the names of the putative email sender, I compare department response rates according
to specific characteristics of the complainant: race/ethnicity (Black, Hispanic and White)
and gender (female and male). I find that departments are less likely to respond to emails
signed with Black and Hispanic names. Differences in response rates become more
pronounced when I interact gender with race/ethnicity. These differences exacerbate the
more-basic problem of a low overall response rate of 67.4 percent. I find little evidence
that either department size or the characteristics of the local population are correlated with
response rates. Results from this experiment support the accusations that local policing
suffers, on average, from issues of bias and transparency.
4
2.1 Overview
Research suggests that police activities likely generate substantial benefits to
society. Benefits can accrue from their direct effect of reducing crime (e.g., Chalfin,
Hansen, Weisburst, & Williams, 2021; Mello, 2019; Weisburd, 2021; Weisburst, 2019b).
Social benefits also can result from less-direct interventions, like a reduction in traffic
fatalities (e.g., DeAngelo & Hansen, 2014). Chalfin and McCrary (2018) argue that
the benefits of policing are so considerable that despite their substantial budgets, many
departments remain underfunded. However, there is a longstanding debate concerning
the impacts that police practices may have on social welfare. Of primary concern is
the presence of bias in police behavior—in particular, racially motivated bias. In 2020,
protests over racially biased policing broke out across the U.S. after officers in the
Minneapolis police department killed George Floyd. Despite the constant presence of
the topic of police reform in the national dialogue, and alarmingly frequent anecdotes
reported in the media, few rigorous studies exist that causally document bias in local
policing (M. R. Smith, Rojek, Petrocelli, & Withrow, 2017).
Biased policing describes the tendency for police to interact with individuals
at a different frequency or in a different manner depending on the sociodemographic
characteristics of these individuals. Police dictate the frequency of interaction via their
decisions about where to police (e.g., patrol routes) and whom they police (e.g., traffic
stops). Conditional on an interaction taking place, the manner in which police conduct
themselves can vary in terms of treatment during the interaction (e.g., use of force), the
resulting outcome (e.g., caution, citation or arrest), or police accountability following an
interaction (e.g., consequences in the event of police misconduct).
A growing body of research highlights the disproportionate burden that policing
can place on people of color in these various contexts. For example, M. K. Chen,
5
Christensen, John, Owens, and Zhuo (2021) find that neighborhoods with larger Black
populations experience a considerably higher police presence. Similarly, there is evidence
that people of color are more likely to be stopped by police (e.g., Bulman, 2019; Gelman,
Fagan, & Kiss, 2007; Pierson et al., 2020). There is also evidence that the result of a
police-citizen interaction depends on the citizen’s race. Numerous studies find that
people of color are more likely to experience the use of force by police (e.g., F. Edwards,
Lee, & Esposito, 2019; Fryer, 2020; Nix, Campbell, Byers, & Alpert, 2017; Ross,
2015). People of color are also more likely to be targeted for traffic citations and asset
forfeitures (e.g., Goncalves & Mello, 2021; Makowsky, Stratmann, & Tabarrok, 2019;
Sances & You, 2017; West, 2018). Research remains limited, however, on biases in
police accountability. Stroube (2021) documents that, in Chicago, formal complaints
made by Black residents were less likely to be sustained than formal complaints made by
White residents. However, most studies that address biased policing, while descriptively
informative, cannot unambiguously attribute causality.
Establishing causality in the context of biased policing is difficult. First,
differences in the frequency of interaction do not necessarily reflect biased policing.
There is the possibility of a systemic selection problem. Consider the scenario where
sociodemographic groups participate in criminal activity at different frequencies. In
this case, unbiased policing could still result in heterogeneous rates of police-citizen
interactions across sociodemographic groups (Fridell, 2017). Second, measuring
biased policing by comparing outcomes for citizens conditional on an interaction with
police does not permit causal inference. Suppose the motivation for police initiating
an interaction with a citizen is biased, even thought outcomes for all police-citizen
interactions are similar. In that case, a naive analysis can obscure the presence of biased
policing (e.g., Knox, Lowe, & Mummolo, 2020; Ross, Winterhalder, & McElreath,
6
2018). Causal identification of bias in police accountability is especially challenging.
Leveraging observational data necessitates substantial assumptions. Consider the problem
of comparing differences in sanctions for officers between White and Black complainants.
One must assume that the reason for the interaction, the conduct during the interaction,
and the actions taken by the complainant after the interaction are approximately identical.
Furthermore, to compare formal complaint outcomes, all complaints need to be filed,
which could be a substantial obstacle (Ba, 2016). Thus, researchers remain divided on
the existence and extent of biased policing (Fridell, 2017; M. R. Smith et al., 2017).1
Furthermore, while some researchers employ research designs that permit causal
inferences, these analyses involve strong assumptions and the vast majority of these
studies rely on self-reported police data. Such reliance on police-reported data can lead to
inconclusive or incorrect conclusions if police departments strategically or unintentionally
under-report or misreport (e.g., Luh, 2019).
In this paper, I estimate the causal effect of bias on police transparency. To
identify this effect, I conduct a field experiment on a sample of 2,134 U.S. police
departments. I created six fictitious citizen identities with three different apparent
races/ethnicities (Black, Hispanic and White) and two apparent genders (male and
female).2 To create an identity, I choose common first and last names that are strongly
associated with a specific race/ethnicity and gender, and create individual email accounts
for each identity. I then use these identities to email each department a request for help in
making a complaint about an officer in that department. I send each police department an
identical email, but with two exceptions. First, I vary the email sender’s name to signal
1While limited, research has made efforts to address these challenges and find evidence of biased
policing (e.g., Antonovics & Knight, 2009; Gelman et al., 2007; Ross, 2015; West, 2018).
2In this paper, I will use “race” as a catchall term for both race (Black and White) and ethnicity
(Hispanic). I am sensitive to the distinction between race and ethnicity, and I chose to collapse the
distinction in this study for simplicity’s sake.
7
race/ethnicity and gender. Second, I vary the sign-off of the email between an amicable
and a curt tone. Police departments respond to 67.5% of these information requests.
Response rates for emails from Black or Hispanic identities are both 10 percentage points
(pp) lower than the response rates for emails from White identities—differences that are
both significant at the 1% level. Emails from White male identities receive the highest
response rate, at 75.8%, marginally higher than the response rate for emails from White
female identities. Response rates signed with Black and Hispanic male identities are 13.9
and 15 pp lower than White male identities and are marginally lower than response rates
for Black and Hispanic female identities. The tone of the sign-off for the email does not
appear to affect response rates either on its own or when interacted with the different
identities.
I use this particular experimental design for several reasons. The challenge of
causally identifying discrimination is not unique to the context of law enforcement.
Over the last decade, correspondence studies, a type of randomized controlled trial
(RCT), have become an increasingly popular tool for researchers studying the presence
of discrimination (Bertrand & Duflo, 2017).3 Emulating the seminal work of Bertrand and
Mullainathan (2004), researchers have used correspondence studies to identify a variety
of types of discrimination (e.g., gender, age, or race) in various contexts (e.g., housing,
medical services). To date, most correspondence studies focus on Black versus White
discrimination, primarily in the context of hiring practices. There are very few audit or
correspondence studies that focus on discrimination in the provision of public services
in the United States (Butler & Broockman, 2011; Einstein & Glick, 2017; Oberfield &
3In a correspondence study, individuals (often fictitious)—who are identical in terms of all observable
characteristics other than the characteristic of interest—apply for a job, service, or good. The researcher
then examines whether the experimentally varied characteristic of interest affects the outcome of the
application or request (Bertrand & Duflo, 2017). The present study uses email instead of the traditional
approach of “snail mail,” and—as explained below—requests assistance from police departments instead of
applying for jobs or making purchases.
8
Incantalupo, 2021; White, Nathan, & Faller, 2015). Considering that marginalized groups,
on average, are more likely to depend on public services, discriminatory practices are of
utmost concern for social planners.
To the best of my knowledge, the only prior correspondence study that concerns
law enforcement agencies is Giulietti, Tonin, and Vlassopoulos (2019). These authors
conduct a correspondence study with a wide range of public institutions. Included in their
list of public institutions are sheriff’s offices. In their study, the authors email the various
public institutions with benign requests for information. The authors vary the identity of
the requesters, using two distinctively black male names and two distinctively white male
names. The authors find that these public institutions (ranging from public libraries to
sheriff’s offices) are less likely to respond to emails from individuals with distinctively
black names. Furthermore, among the various institutions, this effect is most pronounced
for sheriff’s offices.
By using a correspondence study, I overcome two of the main challenges in
studying discrimination in the context of law enforcement: (1) finding causal estimates
(as opposed to mere associations) and (2) avoiding potentially compromised self-
reporting of data collected or provided by law enforcement agencies. Estimates from
properly randomized correspondence studies can be reasonably assumed to be causal. As
mentioned above, the primary obstacles to causal inference in the study of potentially
biased policing arise from systematic selection—by types of people into criminal
activities, and stemming from police discretion concerning with whom they interact. I
avoid these challenges by creating a citizen-initiated police interaction not predicated on a
crime taking place and by designating my outcome of interest as the police department’s
decision to interact with the potential complainant.4
4I use “citizen” as shorthand for “member of the community” and not to imply any formal citizen/
resident alien/ illegal alien distinction.
9
Avoiding the use of administrative data provided by police departments has
significant advantages. First, intentionally or inadvertently, departments can have ongoing
difficulties reporting accurate data (e.g., Luh, 2019)). Second, police data can be a
product of subjective reporting by individual police officers and department-specific
classification conventions.5 Even when police officers honestly record officer conduct,
decisions made in the heat of the moment during any given citizen-officer interaction
could influence how events are recorded. Finally, departments may be unwilling to
disclose “sensitive information.”6
A correspondence study also allows me to use a national sample of police
departments. I use a sample of over 2,000 police departments representing all states
except Hawaii.7 As a result, the measures of biased policing and accountability from this
study represent policing in the United States on average rather than for any specific state,
county, or city. Consequently, inferences made in this study are more likely to reflect
systemic nationwide behavior patterns rather than specific department cultures.
There are two motivations for using requests for a complaint form as the
experiment’s intervention. To start with, I need a plausible reason for interaction to
conduct a correspondence study involving police departments. As emergency responders,
ethical and natural motives for citizen-initiated contact with the police are limited.
Requesting a complaint form is particularly well-suited for a correspondence study. The
average citizen likely does not already know how to lodge a formal complaint, and it is
believable that a citizen would need guidance in the process. Additionally, it follows that
5For instance, PolicingProject.org describes the discrepancies across states in reporting requirements
for officer-initiated stops. RevealNews.org finds that the Washington D.C. police department has a
comparatively loose definition of “resisting arrest.”.
6Weisburst (2019a) does not find evidence of racially biased policing in Dallas. However, Weisburst
hypothesizes that the department’s willingness to disclose its data to researchers might stem from the fact
that the Dallas police do not appear to have a problem with biased policing.
7Hawaii’s exclusion was a result of random selection. Hawaii only has four distinct police departments.
10
a citizen who believes the police have wronged them would be unwilling or reluctant to
talk on the phone or appear at the station in person (e.g., Ba, 2016).
The primary motivation for requesting a complaint form is to examine openness
to police accountability. Research remains limited on police accountability despite its
centrality to conversations surrounding equitable policing. By asking departments for
help in making a complaint about an officer in their department, I explicitly test the
willingness of departments to hold their officers accountable. I explore two measures of
police accountability. First, the overall response rate from this experiment is a descriptive
measure reflecting a citizen’s likelihood of receiving assistance in any complaint process.
Second, by comparing response rates between the different races and genders of the
requesters, I measure the presence of racial or gender bias in the context of police
accountability. Given that citizen complaints are one of the only tools available for
citizens to address police misconduct, it is crucial to understand any obstacles to the use
of these tools—especially racial or gender discrimination.
In addition to establishing causal evidence of biased policing at the national
level, I make several novel contributions. This study is the first correspondence study
employed with local police departments and the first to focus on the potential for police
accountability to be affected by bias. A particularly significant element of this study is
the inclusion of Hispanic identities and gender. The majority of research concerning
biased policing has been concerned with differences between White and Black citizens.
However, as Weitzer (2014) points out, the lack of research on police-citizen interactions
for Hispanics is “particularly puzzling,” especially considering the growing population
of Hispanic Americans. Even independent of race, it is important to understand whether
police tend to discriminate against a particular gender. Additionally, many stereotypes
that may motivate biased policing frequently include the intersection of race/ethnicity and
11
gender. By including both race/ethnicity and gender in my study, I can test correlations
between potentially problematic stereotypes and policing practices.
2.2 Experimental Design and Data
2.2.1 Experiment. In this section, I describe the design, and implementation
of this correspondence study. The objective of the study is to test whether police
departments exhibit signs of racial/ethnic or gender discrimination. In broad strokes,
this study collects contact information for a nationwide sample of police departments in
the U.S. and then emails each departments using one randomly assigned instance from a
specially designed set of complainant “identities” that I create.8
Police Department Selection: The police departments included in this study are a
stratified random sample. For inclusion in the study, I sought police departments that are
associated with a local government (i.e., no state police) and that serve a population of
at least 7,500 people. To assemble my list of police departments, I randomly sampled
local governments, in batches of 1,000, from the universe of local governments provided
by the U.S. Census.9 For my sample of local governments, I searched the internet for
an email address for the corresponding police department; I conducted a separate search
for an email address for each department (i.e., I did not use an LEA directory). Some of
the selected local governments did not have their own local police department, and some
police departments did not have publicly available email addresses. I recorded each of
these outcomes when they occurred and dropped the local government in question from
the study.
8I preregistered this experiment at the AEA RCT Registry, and the pre-analysis plan can be found here.
9I filtered the universe of local governments to exclude states, counties, and all governments with
populations less than 7,500.
12
Through my sampling process, I identified 2,417 local governments with their
own local police department. I could not find publicly available email addresses for
approximately 12% (283) of these departments. Table 1 describes how these 283 “no
email” departments differ from other departments. In the table, I compare the “no email”
departments to (1) all local police departments, (2) local police departments serving
populations of at least 7,500, and (3) the departments in my study for which I was able
to locate email addresses.
Many police departments had multiple publicly available email addresses.
When deciding which address to select, I prioritized the general department email, then
the police chief, and then the next-highest-in-command officer. In the end, I retained
2,134 local police departments as both eligible and able to receive emails, representing
49 states.10 Figure 1 illustrates the proportion of each U.S. state’s population that is
represented by the departments selected for this study. To calculate these proportions, I
summed the local populations served by the selected departments in a state and divided
that sum by the state’s total population. Please refer to Appendix A.1 for more details.
Identity Creation: I use the names of the putative email senders to signal race and
gender. I created six broad categories of identities for this study: Black female, Black
male, Hispanic female, Hispanic male, White female, and White male. Sixty unique first-
name/last-name combinations are specified for each type of identity.
For this study, I selected last names from the “Frequently Occurring Surnames
in the 2010 Census” dataset. I selected last names that were both racially distinctive
and commonly occurring. To select racially distinctive names, I found names highly
concentrated in one racial group—this requires that the name is both common for a
10As noted above, Hawaii’s exclusion from the study was an unintentional result of the sampling process.
13
particular race and uncommon for other races. However, in some cases, the most racially
distinctive names were not commonly used in the United States. I avoided using very
uncommon surnames to avoid arousing the suspicions of the police departments. I
constructed a simple algorithm, described in Appendix A.2, to select sufficiently racially
distinctive and reasonably common names. I selected six last names for each race.
I referred to Gaddis (2017b) and Gaddis (2017a) to select the first names.
Motivated by the frequent use of names as signals for races in audit studies, Gaddis
conducts two experiments that explicitly test which first and last names are racially
distinctive. In these experiments, Gaddis asks subjects which race they associated with
a particular name. Gaddis conducted this experiment for names commonly used to
represent Black people (Gaddis, 2017b) and Hispanic people (Gaddis, 2017a) in audit
studies. I chose the ten most racially distinctive first names for the respective identities
from these two studies. In total, I created 360 unique names (6 identities × 6 last names
× 10 first names). After selecting the names for each identity, I created a unique email
address for each last name used in the study (e.g., olson.2922@examplemail.com).
I then created a unique email address profile for each identity (e.g., Claire Olson
<olson.2922@examplemail.com>). As a result, the full names of the identities
were visible in the email inboxes of the police departments (e.g., Claire Olson
<olson.2922@examplemail.com>).11
The complete list of names can be inferred from Tables 2 and 3 (360 unique name
combinations). I ultimately omitted six high-profile recognizable celebrity names from
my set of 360 names: Denzel Washington, Tyra Banks, DaShawn Jackson, Seth Meyer(s),
Katelyn Olson, and Pedro Martinez. These names have widespread recognition and
11Please refer to Appendix A.3 for details concerning the specific email addresses used.
14
during the testing process, respondents noted that they strongly associated these names
with celebrities having the same name.
Email: Each department then received one email from a single randomly assigned
identity. All these emails were identical with two exceptions (1) the idenity of the email
sender and (2) the sign-off used in the email. I varied the sign-off to test whether the tone
of the email might have any effect on police behavior. I decided to use the sign-off as
the vehicle for this treatment because the sign-off influences the perceived amicability of
the email but minimally alters the content of the email. I randomly assigned the sign-off
across emails. I use the email sender’s name twice in each email to increase the salience
of this information. Each email had the following format:
From: Full name <lastname19xx@mail.com>
Subject: Complaint Assistance
Body:
X Police Department,
My name is first name and I am interested in filing a complaint against an
officer in your department. I am not sure what to do, and would like to
request information on how to make a complaint. Can you please send me
this information?
Sign-off
Full name
The italicized words indicate that these words changed across emails. As
described above, I created profiles for the email accounts so that departments would see
the complainant’s full name twice and their first name three times. Police departments
15
were addressed directly—without, for example, a “Hello”—because I found during the
pretesting process that the inclusion of a salutation increased the chance of the email
being marked as spam. The sign-off varied between a cordial sentiment (“Thank you!”)
and a curt sentiment (“Sincerely,”). Appendix A.4 includes images of example emails and
other details on the design of the email template.
Timing: I conducted the study over a ten-week period, from late June 2022 to late
August 2022. I sent roughly 210 emails each week, split across Monday, Tuesday,
and Wednesday. I sent all emails at approximately 9 a.m. local time for each police
department. I rolled out the experiment over ten weeks to minimize the chance that a
single unanticipated news event would compromise the generalizability of the results.
Splitting the emails across days of the week simply reduced the logistical difficulty of
sending the emails. I did not send emails on Thursday, Friday, or weekend days, to give
departments at least two full weekdays to respond to the inquiry.
Treatment Assignment The “treatment” here is the identity (race and gender) that
each department sees. I stratified treatments by week and by state. As a result, the number
of departments for each state is balanced each week. Treatment was then randomly
assigned across departments within each week-state stratum. Appendix A.5 details the
treatment-assignment process.
2.2.2 Data. I use several additional datasets in this study. As mentioned, I
used data from the US Census to create a pool of local governments in the department-
selection process (U.S. Census Bureau (2021)). I limited the local governments eligible
for inclusion in the study to exclude state and county governments and governments with
16
populations less than 7,500 residents.12 I then matched my selected departments, ex post
of their selection, with databases of police departments from OpenPolice.org and ICPSR
(Lesko, Silverman, & Troup, 2021, April 23; United States & Bureau of Justice Statistics,
2012)).13 These department databases provided information about exact agency locations
and unique official identification numbers.14
The study includes data for several other observable department characteristics.
These characteristics, ex ante, seemed to be potentially important determinants of the
response behaviors of police departments: numbers of officers and civilian employees
for each department; county-level income information; and county-level racial/ethnic
composition. I use the Uniform Crime Reporting (UCR) Program data compiled by
Kaplan (2021) for employee counts for each department. The UCR dataset includes
employee counts through 2020. However, a handful of departments have missing data
for 2020. I use the most-recent employee count since 2010 (for 231 of these departments)
where available. If a department does not have an employee count after 2010, I record
that department’s employee count as missing (29 departments). I compile income and
race data from the 2019 American Community Survey (U.S. Census Bureau, 2019).
In the 1-year ACS data, 148 counties are missing data for the median income of Black
households, and 55 counties are missing data for the median income of Hispanic
households. Police departments selected for the study are associated with governments
smaller than counties. However, it is not clear with exactly which population each
department would interact. If I use data for a geography that is too precise (e.g., the
12During the collection process for police department email addresses, due to multiple instances of
the same state having multiple local governments with the same name, I inadvertently included 117
departments in communities with populations less than 7,500. I nevertheless include these departments
in the study, and demonstrate that the main results are robust to their exclusion.
13These databases did not include email address contact information.
14I collected the Originating Agency Identifier (ORI) numbers for all departments that have ORI. See
Office of Justice’s explanation for details.
17
zip code of the department), I risk mischaracterizing a department’s local context.
Accordingly, I use county-level data to characterize the economic and racial composition
of a department’s environs. I sacrifice some precision with this approach but avoid
inaccuracy.
Table 4 shows relevant department characteristics. Column (1) of the table is
the mean value for each different characteristic for departments that received emails
from White-male identities. Columns (2) through (6) are the differences between the
White-male mean value and the mean values for other identities. Table 4 confirms
that the treatment was successfully randomized across the most obvious department
characteristics relevant to this study. Only one of the 80 differences throughout the rows
and columns is statistically significant, and only at the 10% level (Pop. % Black (county-
level)).
2.3 Results
2.3.1 Summary Statistics. I sent the first emails on Monday, June 27, 2022,
and the last emails on Wednesday, August 31, 2022. In total, I attempted to contact 2,134
police departments. Table 5 summarizes the outcomes of these emails. My final analyses
(below) exclude the 37 emails that were undeliverable (i.e., denied or failed).15
Table 5 indicates a response rate of 66.31%. If I exclude the 37 undeliverable
emails (Denied or Failed), the response rate is 67.48%. This response rate, however, is
aggregated across all correspondent identities and says nothing about biased policing. The
Denied category in column 1 represents emails that were blocked by police departments.
The small number of Denied emails does not cause concern for the experiment’s validity.
15During the experiment, I received “undeliverable” messages from the email server I used. These
“undeliverable” emails explained why the email I sent could not be delivered. In some cases, the email
address I used for a police department was incorrect or no longer existed; these are the “failed” emails. In
other cases, the police department email server blocked my email for some unknown reason; these are the
“denied” emails.
18
However, it is concerning that some police departments have structured their email
server to block a seemingly legitimate request for help. Of course, the request is part
of an experiment, but it is easy to imagine a citizen with a genuine complaint making a
similarly formatted request. The Failed emails are also a cause of concern in terms of
police accountability. Given that I manually collected the email addresses for each police
department from the department’s own website, a Failed email potentially implies that a
department may neglect to maintain updated and accessible contact information.
I summarize department response times in Figure 2. A large majority of responses
from police departments occurred during the first 24 hours after I sent the email, and I
received 97% of the responses within two days. The timing of the responses suggest that
the departments take the request for help seriously. Combining these two results paints
a picture that not all departments are willing to assist the public in making a complaint
against an officer. However, the willing departments engage promptly.16
As mentioned, the study’s emails were sent out in batches over ten weeks to
reduce the chances of current events influencing police department response behavior. In
Appendix A.8, Figure B5 depicts the response rate for all identities by week, and Figure
B6 breaks down the weekly response rates by identity. The figures suggest that response
behavior did not change much over time, at least during the ten weeks of the experiment.
2.3.2 Main results. The primary focus of this study concerns the effect
of racial/ethnic or gender biases on transparency in policing. To this end, I estimate
variations of the following equation:
1(Responsei) = β11(Genderi = Female)+β21(Racei = Black)
+β31(Racei = Hispanic)+FEs,t + εi
16In Appendix A.7, I examine whether response time differs systematically across identities but find no
evidence.
19
Where i indexes individual police departments, t indexes the week the email is sent, and s
indexes a department’s state. The emphasis in this initial analysis concerns the differences
in police department response behaviors to White putative identities and Black/Hispanic
putative identities. Accordingly, the omitted identity in the analysis is either White
or White male. The main outcome for this study, 1(Responsei), is a binary indicator
for whether a police department responded, within four weeks, to an email (I record a
response for a department if that department replies within 28 days.17 FE represents fixed
effects for the week I sent an email and a department’s state. Given that I stratified the
treatment assignment on week and state, I include fixed effects for both week and state
throughout my analyses. Additionally, I cluster the standard errors by week and state.
Table 6 reports the most straightforward analysis of differences in response rates
across identities using two alternative weighting schemes. The two weighting schemes
allow us to infer two different population parameters. The “unweighted” results describe
response rates for an average police department. In other words, if a person were to
contact a randomly selected police department, the unweighted response propensities
(columns 2 and 4) are relevant. However, departments that serve larger populations
interact with more citizens and are thus likely to receive more requests for assistance. By
weighting each observation by that department’s local population (i.e., the population of
its jurisdiction), the response rates shift the interpretation of the key coefficients from the
average department’s behavior to what the average person should expect to encounter.18
17Automatically generated emails from departments merely acknowledging that the treatment email was
received I did not record as responses. I discuss alternative definitions of the response variable below.
18The square root of the population is used as a weight instead of simply the population because of the
large distribution of population sizes. For example, Los Angeles has a population of close to 4 million,
which is over 200 times as large as the median local population (18,000). However, using the standard
method of logging the populations would reduce the disparity between populations too much. The log of
Los Angeles’s population is approximately 15, which is comparatively similar to the log of the median local
population (log(18000)≈ 9.8).
20
Column (1) of Table 6 compares unweighted department response rates for emails
with Hispanic identities (Hispanic emails) and Black identities (Black emails) to the
mean response rate for emails with White identities (White emails). The response rate
for White emails is 74.86%. Compared to the White email response rate, the response
rate for Black emails is 10.42 percentage points (pp) lower [4.33, 16.49], and the response
rate for Hispanic emails is 10.66 pp lower [5.54, 15.77]. Both differentials are statistically
significant at the 1% level.19 Column (2) repeats the comparison in column (1) while
weighting observations by the local population. Estimates across columns (1) and (2)
are effectively identical for Black emails. Weighting by population marginally increases
estimated discrimination against Hispanic emails from 10.66 pp to 11.38 pp [8.48, 14.28].
Columns (3) and (4) compare department response rates for emails with any type
of female identity to the mean response rate for emails with any type of male identity
(66.03%). The unweighted estimate from column (3) shows that females, on average,
were 2.26 pp more likely [-3.92, 8.44] to receive a response. However, the difference is
not statistically significant. Column (4) indicates that when weighting by population, the
response rate difference between females and males shrinks to 0.35 pp [-5.91, 6.60].
2.3.2.1 Interaction Effects. Literature shows that race and gender are often
individually related to discrimination (Bertrand & Duflo, 2017). There is also evidence
that the intersection of race and gender is an essential dimension of discrimination
(e.g., Browne & Misra, 2003; Ifatunji & Harnois, 2016)). The intersectionality of race
and gender also plays a significant role in the criminal justice system (e.g., Doerner &
Demuth, 2010; Steffensmeier, Painter-Davis, & Ulmer, 2017; Steffensmeier, Ulmer,
& Kramer, 1998). Motivated by the significance of race-gender intersectionality in
19Comparison of the coefficients of the response rate for Black emails and the response rate for
Hispanic emails reveals that the estimates are not statistically significant from each other, although each
is individually significantly different from the response rate for White emails.
21
discrimination and the criminal justice system, I test whether intersectionality plays
a role in discriminatory policing. I do so by estimating a specification that defines
(Whitei ×Malei) as the base category and distinguishes five alternative race/ethnicity
and gender combinations, for a mutually exclusive and exhaustive set:
1(Responsei) = β11(Whitei ×Femalei)+β21(Blacki ×Malei)+β31(Blacki ×Femalei)
+β41(Hispanici ×Malei)+β51(Hispanici ×Femalei)+FEs,t + εi
Where each β indicates the difference in response rate for each combination relative to
the omitted (Whitei ×Malei) response rate. I omit White male for two reasons. First,
parameter estimates from this specification distinguish between the groups commonly
discriminated against (e.g., people of color or female) and the group commonly given
preferential treatment (White males). Second, this specification permits the most
straightforward interpretation of results, given that the White male identity has the highest
response rate (75.78) among the six identities.
Column (1) of Table 7 reports the percentage-point differential in response rates
for the five identities compared to the White male identity. Column (2) reports the results
of the same basic specification as column (1) but weights observations by the local
populations of the police departments. Column (1) reveals that response rates for Black
and Hispanic males were significantly lower than White males at the 1% level and are
the lowest among all the identities. Specifically, Black males were 13.94 [6.55, 21.33]
pp less likely to receive a response, and Hispanic males were 15.00 [8.05, 21.94] pp
less likely to receive a response than White males. The corresponding response rates
for females (specifically Black and Hispanic) were higher than their male counterparts
but still significantly lower than White males. Black females were 9.70 [1.92, 17.48] pp
less likely to receive a response than White males and Hispanic females were 9.28 [0.99,
22
17.58] less likely to receive a response than White males. The estimates are statistically
significant at the 5% and 10% levels.
Testing for equality between the coefficients within each race group between
genders finds that the response rates for Black males and Black females are not
statistically significantly different (p-value = 0.3119). In contrast, the response rates for
Hispanic males and females are statistically significantly different (p-value = 0.0035).
The response rate for White females is 2.85 [-6.55, 12.25] percentage points lower than
for White males but the difference is not statistically significant at the 10% level. White
females are the only female identity with a lower response rate point estimate than their
male counterpart within each race/ethnicity grouping. The heterogeneous differences
in response rates for gender, when interacted with race, suggest the importance of
the intersectionality of race and gender. When individuals are White, males receive
preferential treatment. However, this relationship reverses for the Black and Hispanic
groups. Likely, studying discrimination with respect to only race or gender, without
consideration of the other characteristic, may obscure important aspects of the underlying
situation.
Weighting by local populations increases the estimated disparity in the response
rate for White males versus all the other identities, except for Hispanic males. The
response rate for White females in column (2) (6.50 [-4.27, 17.28]) is more than double
the point estimate from column (1) but is still not statistically significant. When I include
local population weights, the response rates for Black females (9.96 [5.20, 14.73]) and
Hispanic females (13.91 [3.81, 24.01]) increase in magnitude and statistical significance.
With these weights, the estimated response rate for Black males (16.71 [7.72, 25.70])
becomes the lowest response rate. The response rate for Hispanic males (14.65 [6.66,
22.64]) decreases marginally but remains statistically significant at the 1% level. In
23
contrast to the estimates in column (1) of Table 7, testing for equality across genders
for the coefficients within each race/ethnicity group suggests that the response rates for
Black males and Black females are statistically significantly different at the 10% level
(p-value = 0.0861). The response rates for Hispanic males and Hispanic females are not
statistically significantly different (p-value = 0.8545).
2.3.2.2 Department Size. Police department response rates likely depend
on the interplay between many factors. Department size, and the population that a
department must serve, could affect response rates by departments. For instance, large
departments might have the option to dedicate staff solely to the task of replying to
requests for help in making complaints. Alternatively, smaller departments might be more
sensitive to officer complaints because each staff member is likely to be more familiar
with all officers in the department. Larger populations being served could mean that
departments have more requests to fulfill. On the other hand, if departments serve small
populations, they might be more familiar with all department activity and therefore more
suspicious of the genuineness of the email they receive.20
Table 8 displays the results of a model that interacts race and gender and defines
(Whitei × Malei) as the base category, like Table 7, but additionally interacts the
race/gender variables with a binary indicator for department size. I use the median
number of total employees for the departments included in the study to determine a
department’s large/small size category. The results reveal that smaller departments
seem to discriminate less against White females and Black males, compared to bigger
departments. The estimated response rate for White females at smaller departments is
almost identical to the White male response rate. Response rates for Black males are
20Several responses mentioned that the police department checked the police logs and had no record of an
interaction with a person that matched the name in the email they received. Consistent with the pre-analyis
plan guidelines, I did not respond.
24
lower than for White males, both for bigger and smaller departments. However, the
point estimates for these two response rate differentials are larger in the case of bigger
departments. For Black males, the response rate differential from bigger departments
increases by 6.97 [19.68, -5.75] percentage points . In contrast to White females and
Black males, Hispanics and Black females have higher response rates when interacting
with bigger departments. Of all the identities, only the response rate for Hispanic males is
significantly different across department sizes.
2.4 Discussion
2.4.1 Interpreting Bias. The results of this field experiment constitute
substantial evidence of racially biased police practices. When aggregated across genders,
compared to White emails, the response rates for Hispanic and Black emails are both
10 percentage points lower and statistically significantly different from White response
rates at the 1% level (Table 6). The question of gender-biased policing is more nuanced
than racially biased policing. When comparing the pooled response rates for males to the
pooled response rates for females, the results suggest that police departments are slightly
more likely to respond to female requests. However, comparing response rates for each
race-by-gender group tells a different story (Table 7). White males receive the highest
rate of response out of all six identities. The low response rates for Hispanic and Black
males drive the lower response rates for all males. Hispanic and Black female response
rates are both about 9 percentage points lower than White males and significant at the
10% and 5% levels, respectively. Comparing the results of Table 6 and Table 7 reveals
that the intersection of race/ethnicity and gender is an essential part of the story. That
Hispanic males receive the lowest response rates of all groups indicates the importance of
expanding research about police-citizen relationships to include Hispanic demographics
(Weitzer (2014)).
25
Identifying the mechanism(s) for the observed hierarchy of response rates of the
six identities is beyond the scope among this paper. However, it is worth considering
why Hispanic males and Black males received the lowest rates of response, despite
White males receiving the highest rate of response. The discrepancy could be explained
by the historical narrative of black and brown males being viewed as criminals (e.g.,
the racist stereotype of the “superpredator”). A common rebuttal to this hypothesis is
that these groups might be more likely to participate in crime—echoing the challenge
researchers encounter when attempting to separate biased policing from different levels of
participation in criminal activities amongst different ethnic/racial groups. However, in the
context of the present study, no crime has been committed. Black and Hispanic males are
simply not treated the same way as their White counterparts.
An alternative explanation for the mechanism behind this discrepancy is that
departments hypothesize that the nature of the complaint might differ across groups.
For instance, research suggests that police are more likely to use excessive force with
people of color (e.g., F. Edwards et al., 2019; Fryer, 2020; Nix et al., 2017; Ross, 2015).
The lower response rates from the present study might reflect that departments think that
complaints from Hispanic and Black males are more likely to concern excessive use of
force from one of their officers. As a result, these departments may avoid assisting the
individual in making a complaint in fear of the consequences should the complaint be
lodged.
Previous work has suggested that documented racial/ethnic discrimination may
reflect bias against poorer or less-educated communities—and race/ethnicity serves as a
proxy for wealth and education (Tilcsik, 2021). For instance, Giulietti et al. (2019) make
an effort to separate the two types of factors in their correspondence study. However, in
practice, this distinction may not matter. The lived experiences of Black and Hispanic
26
populations includes bias—regardless of whether the bias results from racism or classism.
It is likely that police who disproportionately target non-White groups are engaged to
some degree in both statistical targeting and biased policing (Bertrand & Duflo, 2017).
Tilcsik (2021) argues that statistical discrimination “can lead people to view social
stereotyping as useful and acceptable and thus help rationalize and justify discriminatory
decisions.”
2.4.2 Accountability. The primary question this study seeks to answer is
whether police departments discriminate on the basis of race/ethnicity or gender. The
study’s design also emphasizes another critical topic for policymakers interested in
reforming police practices: accountability. The design of this correspondence study
forces police departments to decide whether to respond to an inquiry based solely on a
citizen’s race/ethnicity and gender. However, the study also assesses the willingness of
departments to assist a citizen attempting to hold one of their officers accountable. In
the existing literature, the only prior correspondence study that includes any type of law
enforcement agency is Giulietti et al. (2019). Their correspondence study interacts with
many public institutions, including sheriff’s offices. In their study, the authors email the
various public institutions with requests for relevant but benign information. They use
two black male names and two white male names to vary the identity of the person asking
for information. The authors find that these public institutions (ranging from libraries to
county clerks, in addition to sheriff’s offices) are less likely to respond to email requests
from individuals with distinctively black names. Giulietti et al. find that response rates
for their sheriff’s offices are approximately 53% for White male emails and 46% for
Black male emails. These overall response rates are noticeably lower than the average
response rates in the present study. However, the difference in response rates by race in
the Giulietti et al. study is considerably smaller. One explanation for the difference is that
27
Giulietti et al. target sheriff’s offices instead of local police departments, and sheriff’s
offices may face different expectations for accountability. However, an alternative
explanation is that departments do not treat a simple request for general assistance with
the same urgency as a request for help in making a complaint against a police officer.
When a request for assistance concerns making a complaint, police departments appear
more responsive but may be more likely to discriminate.
It should be noted that average response rates are low in both the Giulietti et al.
study and the present study. The average response rate of 67.4% for the present study
(with a low of 60.6% for Hispanic males) is concerning. Even the most-responded-
to identity, White males, has a response rate of only 75%. By design, the complaints
mentioned in the present study are fictitious. However, in reality, a citizen attempting
to file a formal police complaint suggests potentially serious misconduct on the officer’s
part. Suppose only six out of ten citizens can obtain assistance making a complaint. In
that case, simply a count of citizen-initiated formal complaints about police officers may
not represent a reliable or just basis for holding police officers accountable. This concern
is amplified when groups of people who more frequently interact with police (i.e., people
of color) are also less likely to be assisted in making a complaint.
2.4.3 Caveats. This study seeks to understand whether police departments
tend to discriminate based on race, ethnicity, or gender. The results suggest that police
departments, on average, do discriminate. However, there are a few caveats to this study.
First, police departments were indeed selected randomly (see Appendix A.1). However, a
department was only eligible for inclusion in the study if it had a publicly available email
address. There are likely to be non-random department characteristics that distinguish
between departments that make their email addresses available to the public and those that
do not. In Table 1, I examine how departments without publicly available email addresses
28
differ from other departments. In comparison to the departments I did contact, I find that
these departments tend to have lower income levels, higher shares of poverty (especially
for Black and Hispanic populations), smaller shares of Hispanic residents, and higher
shares of rural residents. In addition, departments on average seem to be smaller–though
the estimates are noisy. Consequently, this study’s results reflect average department
behavior only for a specific type of department. It is plausible that departments willing
to share a contact email might also be more willing to engage with the public. Forty
departments included in the study had contact emails found somewhere other than on the
police department’s official website (e.g., the police chief’s contact information may have
been posted on the city’s website but not on the police department’s own website or the
department’s specific page within the city’s website). The response rate for emails found
in this non-standard way was almost 20 percentage points lower than the overall mean
(47% versus 66%). Drawing clear inferences from such a small sample is challenging.
However, this difference in response rates suggests that departments with easier-to-find
email addresses may be more systematically willing to engage with the public.
Second, this analysis does not seek to identify a fixed effect for each individual
police department. The results demonstrate that, on average, police departments in the
United States have a higher propensity to respond to White emails than Black or Hispanic
ones. However, the data include only one observation per department. Thus it is not
possible to infer systemic bias within individual police departments. Revisiting this type
of RCT with a specific aim of learning more about within-department behavior may be
of value in future studies.21 Finally, one must keep in mind that the conclusions in this
study pertains to a specific context. This study demonstrates that police departments
discriminate on the basis of race/ethnicity or gender when contacted via email for help
21Multiple requests to one department may raise suspicions about the inquiries, however.
29
making a complaint against an officer. It is unclear the extent to which the types of bias
detected in this study are necessarily present in other contexts, for example, a police
officer’s decision to pull over a vehicle.
2.4.4 Conclusion. This study uses a correspondence study to establish strong
causal evidence of biased policing in the United States. Across 2,134 police departments,
departments were 10 percentage points more likely to respond to emails from White
identities than Black or Hispanic identities. Interacting the race/ethnicity and gender of
the identities revealed that White male identities had the highest response rates and Black
male and Hispanic male identities had the lowest response rates—respectively, 13.94
and 15 percentage points lower, respectively, than the White male response rates. The
low overall response rates, and significant bias in responses across identities, are each
concerning. Low response rates suggest police departments resist accountability. Bias
in responding to minority identities suggests that departments are especially unwilling
to engage with communities of color—disproportionately policed communities. While
the existing literature has been inconclusive about the existence of biased policing, the
results of this study suggest that bias in policing does exist and that it may hinder progress
toward police transparency and accountability.
30
2.5 Tables Figures
31
32
Table 1. Comparison of departments included and excluded from experiment
All Departments Departments > 7,500 Searched Departments
Mean Difference Mean Difference Mean Difference
Income (county-level)
Median Income all HH ($1,000s) 59.71 3.5*** (1.02) 67.34 -4.02*** (1.12) 66.61 -3.4** (1.11)
Median Income Black HH ($1,000s) 43.38 2.04 (1.26) 47.6 -1.93 (1.19) 47.67 -2.25 (1.27)
Median Income Hispanic HH ($1,000s) 50.27 0.69 (.095) 53.18 -2.27** (0.87) 52.93 -1.97* (0.89)
Median Income White HH ($1,000s) 64.88 5.41*** (1.11) 74.71 -4.18*** (1.22) 73.64 -3.35** (1.23)
% Pop. in poverty 13.4% -0.6% (0.31%) 12.3% 0.5% (0.29%) 12.2% 0.6%* (0.30%)
% Black pop. in poverty 23.5% 0.3% (1.41%) 21.9% 1.8%** (0.62%) 21.8% 1.9%** (0.65%)
% Hispanic pop. in poverty 21.2% -0.1% (0.67%) 19.6% 1.5%** (0.48%) 19.3% 1.8%*** (0.48%)
% White pop. in poverty 10.4% -1.0%*** (0.26%) 8.8% 0.6%** (0.22%) 8.9% 0.5%* (0.23%)
Population
Local government pop. (hundreds) 18.57 19.6** (6.63) 48.05 -8.37 (11.21) 50.4 -12.23 (10.31)
Pop. % Black (county-level) 9.4% 1.4% (0.75%) 10.4% 0.7% (0.70%) 10.2% 0.6% (0.72%)
Pop. % Hispanic (county-level) 10.8% 1.1% (0.82%) 15.4% -3.4%*** (0.98%) 14.1% -2.2%* (0.92%)
Pop. % White (county-level) 73.7% -3.3%** (1.17%) 66.3% 3.5%** (1.25%) 68.2% 2.2% (1.25%)
Pop. % rural (county-level) 38.7% -15.4%*** (1.83%) 18.5% 4.2%*** (1.22%) 20.2% 3.1%* (1.28%)
Department size (# of employees)
Total employees 44.78 35.46 (31.04) 113.97 -30.96 (53.18) 128.81 -48.57 (34.16)
Total officers 35.48 27.72 (22.32) 89.45 -24.12 (38.21) 103.47 -40.27 (28.79)
Total civilian employees 9.3 7.74 (9.16) 24.52 -6.84 (15.72) 25.34 -8.3 (6.13)
This table compares mean values of geographic and police departmental characteristics to the police departments for which I was not able
to find a publicly available email address. There are 283 “no email” departments. Mean indicates the average value for all departments and
Difference indicates the differential from the mean for departments without email addresses. The first two columns report the mean for all police
departments (n = 12,523) in the U.S. to the departments without publicly available email addresses. The next two columns report the mean for
police departments in the U.S. with local populations ≥ 7,500 (n = 4,575) to the departments without publicly available email addresses. The
last two columns report the mean for police departments include in my original sample (n = 2,417) to the departments without publicly available
email addresses. See Appendix A.1 for details on sampling procedure. Standard-errors in parentheses. Signif. Codes: *: 0.5, **: 0.1, ***: <0.1
Table 2. Identity Creation: Last names used in study
White Black Hispanic
Olson Washington Hernandez
Schmidt Jefferson Gonzalez
Meyer Jackson Rodriguez
Snyder Joseph Ramirez
Hansen Williams Martinez
Larson Banks Lopez
33
34
Table 3. Identity Creation: First names used in study
White Male White Female Black Male Black Female Hispanic Male Hispanic Female
Hunter Katelyn DaShawn Tanisha Alejandro Mariana
Jake Claire Tremayne Lakisha Pedro Guadalupe
Seth Laurie Jamal Janae Santiago Isabella
Zachary Stephanie DaQuan Tamika Luis Esmeralda
Todd Abigail DeAndre Latoya Esteban Jimena
Matthew Megan Tyrone Tyra Pablo Alejandra
Logan Kristen Keyshawn Ebony Rodrigo Valeria
Ryan Emily Denzel Denisha Felipe Lucia
Dustin Sarah Latrell Taniya Juan Florencia
Brett Molly Jayvon Heaven Fernando Juanita
35
Table 4. Balance Table
Putative Identity
(1) (2) (3) (4) (5) (6)
White Male White Female Hispanic Male Hispanic Female Black Male Black Female
(n = 359) (n = 352) (n = 350) (n = 361) (n = 358) (n = 354)
(Mean) Differential
Income (county-level)
Median Income all HH (hundreds of dollars) $667 -0.3 (13) 0.7 (13) -5 (13) 3.4 (13) -1 (13)
Median Income Black HH (hundreds of dollars) $477 -19 (15) 5 (15) -1.7 (15) 6.3 (15) 7.6 (15)
Median Income Hispanic HH (hundreds of dollars) $531 -6.8 (10) 3.3 (10) -6.8 (10) -2.7 (10) 4.8 (10)
Median Income White HH (hundreds of dollars) $733 9.6 (14) 6.8 (15) -12 (14) 3.4 (14) 3.5 (14)
% Pop. in poverty 12 0.39 (0.36) 0.40 (0.36) 0.12 (0.35) -0.11 (0.35) 0.21 (0.36)
% Black pop. in poverty 22 0.90 (0.76) -0.07 (0.77) -0.20 (0.76) -0.61 (0.76) 0.33 (0.76)
% Hispanic pop. in poverty 19 -0.04 (0.56) 0.25 (0.57) 0.13 (0.56) 0.00 > (0.56) -0.16 (0.56)
% White pop. in poverty 9 0.06 (0.27) 0.08 (0.27) -0.06 (0.27) -0.17 (0.27) 0.02 (0.27)
Population
Local government pop. (hundreds) 491 41 (128) -11 (128) 130 (127) -104 (127) 17 (127)
Pop. % Black (county-level) 10 1.57* (0.84) 0.19 (0.85) 0.64 (0.84) 0.07 (0.84) 0.84 (0.84)
Pop. % Hispanic (county-level) 14 -0.21 (1.11) 0.72 (1.11) 0.37 (1.10) 0.16 (1.11) 0.33 (1.11)
Pop. % White (county-level) 69 -1.99 (1.48) -1.15 (1.48) -1.32 (1.47) -0.23 (1.47) -1.67 (1.48)
Pop. % rural (county-level) 21 -2.19 (1.51) -1.29 (1.51) -0.69 (1.50) 0.61 (1.50) -0.43 (1.51)
Department size (# of employees)
Total employees 128 -1 (43) -13 (43) 48 (43) -22 (43) -8 (43)
Total officers 104 -1 (36) -12 (36) 40 (36) -22 (36) -9 (36)
Total civilian employees 24 0 (8) -1 (8) 8 (8) 0 (8) 1 (8)
This table compares mean values of geographic and police departmental characteristics across the different identities. For each variable being compared,
Column 1 displays the mean value of the variables for departments that received emails from White male identities. Columns 2 through 6 show the difference
between the value in Column 1 and the mean value for the other five identities. For example, the average county median income for departments that received
emails from White male identities is $66,700. In comparison, the average county median income for departments that received emails from Black female
identities is $100 lower, with a standard error of $1,300. The absence of strongly statistically significant differences across the table reflects that the variables
are not correlated with treatment assignment. 117 departments served local populations < 7,500. Department size data was missing for 29 departments, and
department size data for the year 2020 was missing for an additional 231 departments. 148 observations were missing for median income of Black hh and 55
observations were missing for median income for Hispanic hh in each department’s county. Standard-errors in parentheses. Signif. Codes: *: 0.1
Table 5. Emails Categorized by Outcome
Email Outcome Total Percent of Total
Single Response 1,226 57.45%
Multiple Response 189 8.86%
No Response 682 31.96%
Denied 15 0.70%
Failed 22 1.03%
Sent 2,134 100.00%
I categorize each email by its outcome. The results
show an overall response rate of 66.3% (57.45 +
8.86). Thirty-seven emails were undelivered because
the police department’s address was incorrect (failed)
or police departments blocked the emails (denied).
The response is slightly higher (67.5%) if I drop the
37 undeliverable emails from the calculation. Of the
1,415 departments that responded, 189 departments
sent multiple emails.
36
Table 6. Response Rate Differences by Race and Gender
Dependent Variable: Response
Model: (1) (2) (3) (4)
Variables
Black -0.1042∗∗∗ -0.1041∗∗∗
(0.0310) (0.0285)
Hispanic -0.1066∗∗∗ -0.1138∗∗∗
(0.0261) (0.0148)
Female 0.0226 0.0035
(0.0315) (0.0319)
Fixed-effects
Week Yes Yes Yes Yes
State Yes Yes Yes Yes
Weights
None Sqrt of local pop. None Sqrt of local pop.
Fit statistics
Observations 2,095 2,095 2,095 2,095
R2 0.05993 0.06897 0.04937 0.05700
Within R2 0.01171 0.01271 0.00061 0.00001
Clustered (Week & State) standard-errors in parentheses
Signif. Codes: ***: 0.01, **: 0.05, *: 0.1
I compare differences in response rates for races and genders, unweighted and weighted
by local population. Black and Hispanic identities were less likely to receive responses
from police departments than White identities. Black and Hispanic response rates were,
respectively, 10.42 pp and 10.66 pp lower than the White response rate (74.82)—both
significant at the 1% level. Females were marginally more likely, 2.23 pp, to receive
responses than males (66.02).
37
Table 7. Response Rate Differences for Race and Gender Interactions
Dependent Variable: Response
Reference group mean
White male 0.7578
Model: (1) (2)
Variables
White × Female -0.0285 -0.0650
(0.0479) (0.0550)
Hispanic × Male -0.1500∗∗∗ -0.1465∗∗∗
(0.0354) (0.0408)
Hispanic × Female -0.0928∗ -0.1391∗∗
(0.0423) (0.0515)
Black × Male -0.1394∗∗∗ -0.1671∗∗∗
(0.0377) (0.0459)
Black × Female -0.0970∗∗ -0.0996∗∗∗
(0.0397) (0.0243)
Weights
Standard OLS Sqrt of local pop.
Fixed-effects
Week Yes Yes
State Yes Yes
Fit statistics
Observations 2,095 1,979
R2 0.06214 0.07374
Within R2 0.01404 0.01526
Clustered (Week & State) standard-errors in parentheses
Signif. Codes: ***: 0.01, **: 0.05, *: 0.1
Results display the difference in response rate for each identity compared to White males.
The White male response rate of 75.78 is the highest, and I use it as the control group.
Model 2 has the exact specification as Model 1 but weights observations by the size of
the local population for each department. Black and Hispanic males were the least likely
to receive responses from police departments. Black and Hispanic females also have
lower response rates than White males, but the magnitude and statistical significance of
the estimates are not as large as their male counterparts. White females are marginally
less likely to receive responses than White males, but the differences are not statistically
significant.
38
Table 8. Department Size Heterogeneity
Dependent Variable: Response
Model: (1)
Variables
White × Female -0.0008
(0.0568)
Hispanic × Male -0.1808∗∗∗
(0.0406)
Hispanic × Female -0.1125∗
(0.0503)
Black × Male -0.1070∗∗
(0.0350)
Black × Female -0.1068∗
(0.0526)
White × Female × Big_agency -0.0543
(0.0473)
Hispanic × Male × Big_agency 0.0723∗∗
(0.0272)
Hispanic × Female × Big_agency 0.0503
(0.0652)
Black × Male × Big_agency -0.0697
(0.0649)
Black × Female × Big_agency 0.0211
(0.0447)
Fixed-effects
Week Yes
State Yes
Fit statistics
Observations 2,066
R2 0.06669
Within R2 0.01700
Clustered (Week & State) standard-errors in parentheses
Signif. Codes: ***: 0.01, **: 0.05, *: 0.1
Notes. I create a binary indicator for department size, dictated by the median department
size. I compare response rates for each identity to the White male response rate. Black
males and White females have comparatively lower response rates when interacting with
“bigger” departments. In contrast, Hispanic females and males, and Black females have
comparatively higher response rates when interacting with “bigger” departments. The
only statistically different response rate across department sizes is for Hispanic males.
39
AK ME
VT NH
Pop. Served by Depts.
TX (77.6%)
WA MT ND MN WI MI NY MA RI
70%
ID WY SD IA IL IN OH PA NJ CT 60%
50%
OR NV UT NE MO KY WV MD DE DC
40%
CA AZ CO KS AR TN VA NC 30%
20%
NM OK LA MS AL SC
KY (10.8%)
TX GA
HI FL
Figure 1. Department Selection Heat Map
The figure portrays the proportion of each state’s population represented by the local
police departments I contacted. To calculate the proportion, I summed the local
populations for each included local police department in a state and then divided that
sum by the state’s total population. The state with the lowest representation was Kentucky
( 11%), and the state with the highest representation was Texas ( 77%)
40
Figure 2. Response time summary
I bin the number of responses by response time. I received most of the responses (809)
within three hours of initial contact. Out of all the responses, I received 97% within 48
hours of contacting the departments. I received two emails outside the 4 week window,
and I decided to record these emails as non-responses, because I deemed 4 weeks too
long of a wait time to be considered helpful.
41
CHAPTER III
PUBLIC PREFERENCES FOR A STATE-LEVEL CARBON CAP-AND-TRADE
PROGRAM
The survey described in this chapter was developed by Trudy Ann Cameron and
me, with helpful input from family, friends and colleagues.
We report upon the results from a set of survey-based choice experiments
designed to assess state-level demand for carbon cap-and-trade programs with different
attributes. The evidence from 1050 respondents confirms that these state-level preferences
are strongly heterogeneous with respect to political ideologies and opinions about
climate change. Our models allow us to calculate the implied social benefits of carbon
emissions reductions. Our SBC measure complements existing measures of climate
mitigation benefits based on the social cost of carbon (the SCC, which is an avoided-
cost measure, as opposed to a willingness-to-pay measure). Willingness to bear the
household costs of a cap-and-trade program is affected by the extent of carbon emissions
reductions the program would provide, but also by the changes in the number of jobs
in carbon-intensive industries and in “green” industries. We estimate the marginal rate
of substitution between “carbon” jobs and “green” jobs for different preference classes.
There is heterogeneity in the extent to which the share of permits auctioned, or the uses
of auction revenue, affect demand, and evidence of the extent to which people would
prefer a program that includes additional regulations to limit co-pollutant emissions by
firms that buy carbon permits to cover increased carbon emissions. Methodologically, we
account for systematic sample selection of respondents relative to the quota-driven sample
of invitees from our internet panel, and we net out the effects of earlier randomized choice
scenarios on later choices by the same respondent.
42
3.1 Introduction
Even as the destructive effects attributed to climate change intensify
(Intergovernmental Panel on Climate Change (IPCC) (2018) Intergovernmental Panel
on Climate Change (IPCC) (2021)), the United States remains polarized about climate
change policy (Egan and Mullin (2017)). Optimal design and successful implementation
of carbon mitigation policy has proven to be exceedingly difficult and a subject of
cardinal importance (Aldy and Pizer (2009)). Carbon pricing is often touted as the
economically efficient and potentially politically feasible solution to the carbon emission
crisis (e.g. Metcalf (2009), Y. Chen and Hafstead (2019) ). Carbon cap-and-trade
programs have thus gained traction as a leading tool for climate change mitigation
(Newell, Pizer, and Raimi (2014), Raymond (2019)).
Regional carbon cap-and-trade programs have been adopted, but the United States
has yet to launch such a program at the federal level (see Schmalensee and Stavins (2017)
for discussion). The increasingly urgent need for mitigation policy, along with federal
inaction, may necessitate that regional coalitions or individual states, other than just
California, implement policies at a sub-federal level (Fullerton and Karney (2018)). In
2019 and 2020, Oregon’s legislature twice attempted, unsuccessfully, to create a carbon
cap-and-trade program. Oregon’s attempts and failure to launch such a program highlight
the complicated and contentious political, environmental, and social concerns regarding
environmental regulation (Farber (2012), Deryugina, Fullerton, and Pizer (2019) and
Fowlie, Walker, and Wooley (2020)). Successful passage of a carbon cap-and-trade
program for Oregon, and in other states, will rely on the extent to which policy makers
understand population preferences for a number of key program attributes.
Lack of support for carbon cap-and-trade programs could be the product of a
number of different factors. For instance, conservative politicians who oppose many
types of regulations have employed the phrase “job-killing regulations” to sour the
43
public against programs like cap-and-trade, despite a lack of conclusive evidence from
existing programs (Coglianese, Finkel, and Carrigan (2013)). Additionally, market-based
carbon emission solutions, like cap-and-trade, have been criticized for their inattention to
distributional impacts (e.g. Fullerton and Muehlegger (2019), Goulder, Hafstead, Kim,
and Long (2019) W. A. Pizer and Sexton (2019), and Feger and Radulescu (2020)).
A number of the papers in the literature have found evidence that carbon pricing can
be regressive (e.g. Burtraw, Sweeney, and Walls (2009), C. A. Grainger and Kolstad
(2010), and Moz-Christofoletti and Pereda (2021)).1 Carbon cap-and-trade programs
also raise environmental justice concerns with respect to their distributional effects
(Kaswan (2008), Farber (2012)). To date, these theoretically possible concerns have
been largely unsubstantiated (e.g. [Fowlie, Holland, and Mansur (2012), C. M. Anderson,
Kissel, Field, and Mach (2018) and Hernandez-Cortes and Meng (2020)). They remain an
impediment nonetheless.
The biggest obstacle to public support may simply be partisanship. A review of
climate change opinion surveys in the United States by Egan and Mullin (2017) finds
that not only is partisanship the paramount driver in support of carbon-reduction policies,
but the gap between Republicans and Democrats has become even more pronounced in
recent years. This assessment has been corroborated using revealed preference precinct-
level voting data (e.g. S. Anderson, Marinescu, and Shor (2019)). This partisan division
appears to be due, at least in part, to a considerable effort on the part of corporations
fostering opposition to climate policies through misinformation campaigns (Farrell
(2016), Westervelt (2018)). A better understanding of the factors that affect willingness to
pursue these programs is necessary if policy makers are to design a carbon cap-and-trade
program that has adequate public support.
1Carbon pricing policies also have the potential to be regressive in their benefits (Fullerton (2011)).
44
In this study, we conduct a stated-preference survey to measure individual
preferences for key attributes of carbon cap-and-trade programs. Using randomized
choice experiments in an online survey, we collect a quota-based sample of about 1,000
Oregonians. Each survey asks respondents to consider six unique cap-and-trade programs.
In each choice scenario, the respondent can cast an advisory vote in favor of the program
or to keep the status quo (i.e. no program). We then use these six votes per person to
estimate a random utility model. The marginal utilities estimated for this model allow
us to calculate individuals’ marginal willingness to pay (MWTP) for various program
attributes. Importantly, the survey also collects sociodemographic information about each
respondent. This enables us to infer differences in MWTP for programs with different
attributes across different sociodemographic groups (e.g. income levels, zip codes,
and political ideologies). Another advantage of our study is we are able to measure
key sociodemographic characteristics for quota-screened and eligible respondents who
subsequently drop out of the survey, which allows us to undertake systematic sample
selection correction.2
The present study makes contributions to a number of different veins of research
in the broader literature.3 First, we make a contribution to the growing field of literature
that has used stated-preference studies to understand public preferences for carbon pricing
policies. Carattini, Carvalho, and Fankhauser (2018) provide a survey of recent stated-
preference work aimed at understanding public opposition to carbon pricing.4 The bulk
2The survey screens potential respondents against quotas, so we learn the age, race, gender, income
level, and zip code of every respondent before the respondent learns the topic of the survey.
3Appendix B.1 provides more-detailed reviews of other papers in the related literature. Here, we merely
summarize these papers by group.
4Other examples of stated preference studies that focus on preferences regarding carbon pricing include
Berrens, Bohara, Jenkins-Smith, Silva, and Weimer (2004), Aldy, Kotchen, and Leiserowitz (2012),
Kotchen, Boyle, and Leiserowitz (2013), Duan, Lü, and Li (2014), Yang, Zou, Lin, Wu, and Wang (2014),
Gevrek and Uyduranoglu (2015), Raux, Croissant, and Pons (2015), C. Y. Lee and Heo (2016), Tvinnereim,
Fløttum, Gjerstad, Johannesson, and Nordø (2017), Li et al. (2019), Rotaris and Danielis (2019), Böhringer
et al. (2020), and Daziano, Waygood, Patterson, Feinberg, and Wang (2021).
45
of the extant literature focuses on carbon taxes or undefined carbon reduction policies
(Raymond, 2019). For instance, Kotchen, Turk, and Leiserowitz (2017) conducted a
survey of Americans to measure the WTP for a carbon tax as well as preferences for
how the tax revenue is spent. Their results indicate a substantial mean WTP ($177 per
year). Additionally, 80% of the respondents indicated they would be in favor of using the
revenue to fund green projects and 70% were in favor of using the revenue to support
the a “just transition” for coal workers. Carattini, Baranzini, Thalmann, Varone, and
Vöhringer (2017) use a recent ballot initiative for context in a follow-up stated-preference
survey. They focus on a carbon tax and find lump sum redistribution of tax revenue
and “social cushioning” to be popular. They also find that including more information
improves the acceptability of the policy.
Research has found that revenue recycling, and providing the public with tangible
public benefits, could significantly improve support for carbon pricing (Amdur, Rabe,
and Borick (2014), Beiser-McGrath and Bernauer (2019). In a similar vein, some
national-level studies have focused on measuring preferences for the distribution of costs
imposed by a climate change policy (e.g. J. J. Lee and Cameron (2008), Cai, Cameron,
and Gerdes (2010) ). Brannlund and Persson (2012) use an internet-based survey in
Sweden to measure preferences concerning an unspecified carbon pricing policy. They
described policy alternatives in terms of (a) their development of green tech, (b) their
ability to increase climate change awareness, (c) their monthly cost, (d) their distribution
of costs, and (e) their geographic distribution of carbon reductions. They find that their
respondents prefer policies that are (a) progressive, (b) have lower costs, and (c) raise
awareness for climate change. On the other hand, Baranzini and Carattini (2017) conduct
a qualitative-quantitative hybrid survey and find that individuals are more concerned
about the environmental effectiveness of a carbon tax than with the distributional
challenges that result, or the potential effects of the tax on firm competitiveness. It is
46
likely that public preferences for carbon policies differ dramatically across contexts and
geography.
In general, studies have avoided asking the public about a detailed carbon cap-
and-trade program (e.g. Alberini, Ščasný, and Bigano (2018)). However, there have been
a few studies that have asked respondents about cap-and-trade programs. For instance,
Kotchen et al. (2013) conducted a stated-preference survey that measured WTP for
carbon reduction across different policy instruments (e.g. carbon tax, cap-and-trade,
and a "policy to regulate carbon dioxide as a pollutant") and find no preference across
instruments. However, their survey does relatively little to inform respondents about
the various difference between these policies. Choi, Gössling, and Ritchie (2018) and
Baranzini, Borzykowski, and Carattini (2018) conduct surveys that focus on “offset”
preferences, where offsets are one aspect of many carbon cap-and-trade programs.
To the best of our knowledge, the present study constitutes the most-detailed
analysis of preferences for different possible attributes of alternative carbon cap-and-trade
programs. Considering the leading role that carbon cap-and-trade programs are presently
taking in climate change policy, this is an important contribution.
We also contribute to the body of work that measures public opinion regarding
carbon policy at the state level (e.g. Holian and Kahn (2015), Burkhardt and Chan
(2017), and S. Anderson et al. (2019)). S. Anderson et al. (2019) use voting data from
two failed carbon tax bills in Washington State and find that political party affiliation
is by far the biggest indicator of support or opposition to the policies, with political
ideology accounting for 91% of the variation in vote shares across precincts. This finding
is consistent with the broad review of climate change opinion surveys by Egan and Mullin
(2017). While we rely on hypothetical advisory votes, we advance these studies by using
individual-level data, rather than precinct-level data. This involves less measurement error
47
than would be involved with the use of precinct-level averages as a proxy for individual
characteristics.
Our study has the added benefit of measuring climate change policy opinions
in a state (Oregon) that has recently experienced an onslaught of extreme temperatures
and serious wildfires that are most likely attributable, at least in part, to the effects of
climate change on long-term drought conditions. Using zip code information, we can
match respondents to their local context, including local weather-related conditions,
recent drought conditions, and wildfire exposure. This permits us to estimate the effects
of exposure to some likely consequences of climate change on respondents’ preferences
for climate-change mitigation policy. This aspect of our analysis complements other work
measuring the exposure effect (e.g. Spence, Poortinga, Butler, and Pidgeon (2011), Bain,
Hornsey, Bongiorno, and Jeffries (2012), and Scannell and Gifford (2013)).
3.2 Basic Choice Model
3.2.1 Homogeneous preferences. Our choice experiments describe each
potential cap-and-trade program in terms of nine attributes: (1) the monthly cost per
household; (2) the percent change in carbon emissions (all negative); (3) the percent
change in carbon-industry jobs (all negative); (4) the percent change in green-industry
jobs (all positive); (5) the percent of carbon emissions permits that would be auctioned
to firms, rather than given away for free; (6)the percent of auction revenue that would
be used to fund equipment/machinery as the economy adapt to carbon pricing; (7) the
percent of auction revenue that would be used to help displaced workers or affected
communities adapt to carbon pricing; (8) the percent of auction revenue that would be
placed into the state’s General Fund to replace existing taxes; and finally, (9) whether
the program would include additional regulations on other co-pollutants, to prevent their
levels from increasing around firms that may buy enough carbon permits to allow their
emissions of carbon (and other co-pollutants) to increase.
48
Our model is based on the indirect utility of respondent i under carbon cap-and-
trade Program A. Similar to the usual specification for a public policy choice model in the
stated-preference literature, our simplest model is linear and additively separable in the
attributes for each program:
V Ai = β1(Yi −CAi )−β2(%∆carbon emissions)Ai (3.1)
+β3(%∆carbon jobs)Ai +β4(%∆green jobs)
A
i
+β5(%permits auctioned)Ai +β6(%revenue to equip)
A
i
+β7(%revenue to workers)Ai +β81(pollution regs)
A A
i +ηi ,
Note that since the three percentages of auction revenue sum to 100, so we designate
the percent of permit auction revenue going to the state’s General Fund as the omitted
category, with this share determined by the percentages not destined for the other two
uses.
Indirect utility for respondent i under the status quo, V Ni , involves no policy and
therefore no decrease in household income, no carbon reduction, no changes in the
numbers of carbon jobs or green jobs in the respondent’s county, no auctioned permits
and therefore no permit auction revenue to spend on equipment, workers, or to provide
tax relief, and no extra regulations to prevent increases in local pollution. However,
most researchers allow for some “inertia” associated with the status quo, and include a
status quo indicator variable, SQN = 1 for the No Program alternative, where SQA = 0
(implicitly) in equation (3.1) . This utility for the No Program alternative is given simply
by:
V Ni = β1Yi +β9SQ
N +ηNi , (3.2)
since none of the features of Program A will be experienced.
Each respondent’s choice between policy A and the status quo is determined by
whether policy A yields greater utility. Let ∆V A = V Ai i −V Ni be the difference in indirect
49
utilities for respondent i from policy A and the status quo option N, so that policy A is
chosen if and only if V Ai ≥ V Ni or ∆V Ai > 0. Individual i’s baseline level of income drops
out, so our simplest linear-in-variables econometric specification is as follows.
∆V A Ai = β1(−Ci )+β2(%∆carbon emissions)Ai (3.3)
+β3(%∆carbon jobs)Ai +β4(%∆green jobs)
A
i
+β (%permits auctioned)A +β (%revenue to equip)A5 i 6 i
+β7(%revenue to workers)Ai +β81(pollution regs)
A N A
i −β9SQ + εi ,
where εA = ηA −ηNi i i , an error term that is mean-zero.
The respondent is presumed to know their true utility for a specific program, and
will vote for Program A if the utility difference, ∆V Ai , is positive, and to vote against
Program A if the utility difference is negative. The researcher, however, does not observe
εAi . The assumed distribution for this random error term determines the functional form of
the log-likelihood function used to estimate the preference parameter vector (β1, ...,β10)
in equation (3.6) via maximum likelihood methods.
If each individual in the sample is presented with t = 1, ...,T choices, the joint
probability (likelihood) function for this con(ditional logit mo)del is then given by
N T J yit jexp(V jt)
L (β) = ∏∏∏ iJ kt (3.4)
i=1 t=1 j=1 ∑k=1 exp(Vi )
where yit j = 1 if alternative j is chosen and is zero otherwise. To yield a unique set
of parameter estimates, it is necessary to normalize by differencing utility relative to a
numeraire alternative—the No Program option in our case. For the numeraire alternative,
the utility differences is zero so that term (in the ratio becomes ex)p(0) = 1:
N T J ∆ jt
yit j
∏∏∏ exp( V )L (β) = iJ−1 kt (3.5)
i=1 t=1 j=1 1+∑k=1 exp(∆Vi )
In our data, there are only two alternatives in each choice set, but T = 6 choice sets: j1 =
(A,N), j2 = (B,N), j3 = (C,N), j4 = (D,N), j5 = (E,N), j6 = (F,N). Thus the function
50
is even simpler for each choice occasion whe(n J = 2 (a binary)conditional logit model):5
N T J y∆ jt it j∏∏∏ exp( V )L (β) = i kt (3.6)
i=1 t=1 j=1 1+ exp(∆Vi )
The fitted model can be used to solve for each respondent’s marginal willingness to
pay (WTP) for each of the policy attributes described in our choice tasks. For the
homogeneous-preferences specification in equation (3.6), we set the utility difference,
∆V A, equal to zero and solve for the program cost, CA∗i , that would make their
representative individual indifferent between paying the cost and enjoying the benefits
of the program, or keeping the money and doing without the program. This maximum
total willingness to pay for a policy with a specified set of characteristics will be given by:
A β̂
ŴT Pi =C
A∗ 2
i = (%∆carbon emissions)
A
i (3.7)β̂1
β̂3 β̂%∆carbon jobs A 4+ ( )i + (%∆green jobs)
A
β̂1 β̂
i
1
β̂5 β̂
+ (%permits auctioned 6)Ai + (%revenue to equip)
A
β̂ β̂ i1 1
β̂7 %revenue to workers A
β̂8
+ ( )i + 1(pollution regs)
A
i −β9(−1)β̂1 β̂1
where in the difference between any program and the status quo, ∆SQN = −1 for any
active program. We take advantage of the mean-zero error term and predict WT PAi at the
mean error.6
The parameters in this random utility model, when estimated by maximum
likelihood, are distributed asymptotically joint normal (typically with non-zero
covariances). Willingness to pay estimates, therefore, rely on one of several methods for
5The model is only slightly more complex if there is more than one choice set for each individual and
we wish to accommodate similarities among the choices for any given individual.
6The negative sign on the cost term in equation (3.6) means that after we set the utility-difference to zero
and subtract cost term from both side, the negative sign conveniently cancels.
51
accommodating the fact that the ratio of two normally distributed random variables has a
mean that is undefined. Researchers often use the Krinsky and Robb (1986) parametric
bootstrap simulation method, which relies on a large number of random draws from
the joint distribution of the estimated parameter vector, with each draw being used to
calculate marginal WTP for a given attribute, or total WTP (TWTP) for a specified
program, according to the formula in equation (3.7). Over the large number of draws, a
sampling distribution is built up for ŴT P. Descriptive statistics for the distribution of
individual WTP function coefficients, or for total WTP, are calculated across all these
random draws. Researchers typically use the mean and median, and the 90 or 95%
interval, which function as point estimates and an interval measure for predicted marginal
WTP for each program attribute in equation (3.7), or for total WTP.7
Marginal willingnesses to pay for each program attribute are simply one type of
marginal rate of substitution that can be estimated using this choice model. Marginal rates
of substitution between attributes A and B are given by the negative of the ratio of the
marginal utilities for each attribute.8 Equation (3.6) can likewise be used to quantify other
types of tradeoffs that people are willing to make in considering carbon cap-and-trade
policies, not just the tradeoff between income and the the other attributes of the program.
For example, another politically important feature of all these cap-and-trade
programs is that they result in a loss of jobs in the carbon-intensive sector. Rather than
thinking about willingness to pay (i.e. willingness to put up with higher costs for more
7Some alternative strategies for deriving interval estimates for either some marginal WTP or for TWTP
include the delta method and Fieller’s method. Hole (2007) developed an add-in for Stata (wtp.ado) that can
calculate marginal WTP measures in clogit models that are linear and additively separable. Another Stata
add-in (wtpcikr) supports models that are either linear or logarithmic in the additively separable net income
variable and can be used following probit, logit or bivariate probit commands.
8For the WTP calculations, cost CAi is technically the attribute of the program, but we model net income
as the factor that drives utility for the consumer. The marginal rate of substitution between program
attributes and net income (Yi − CAi ) is positive, although the marginal rate of substitution between program
attributes and cost itself (CAi , a “bad”) would be negative, since more of some desirable attribute would be
required to make up for a higher cost.
52
of each other attribute), we can instead think about willingness to incur job losses in the
carbon sector to enjoy the benefits of the policy. We could again set the utility difference
equal to zero and solve for the (% carbon jobs lost)Ai that would make people just
indifferent between getting the carbon cap-and-trade program and its carbon-reduction
benefits, along with those job losses, or forgoing the program and protecting those jobs.
Willingness to swap (WTS) carbon-intensive jobs for a carbon-reduction program with a
given set of other attributes could be calculated as:
β̂ β̂ β̂
WT S(%∆carbon jobs A 1 CA − 2 4)i = ( i ) (%∆carbon emissions)Ai − (%∆green jobs)Aβ̂ β̂ β̂ i3 3 3
− β̂5 β̂(%permits auctioned)Ai −
6
(%revenue to equip)A
β̂ β̂ i3 3
− β̂7 β̂(%revenue to workers)Ai −
8 1(pollution regs)A
β̂ β̂ i3 3
It can be challenging to keep track of the signs on the variables in the data and how
these interact with the signs on the marginal utilities that are specifically associated
with increases in these variables. For example, all cap-and-trade programs offered in the
survey have (%∆carbon emissions)Ai < 0 and (%∆carbon jobs)Ai < 0). But they likewise
have (%∆green jobs)Ai > 0. The marginal utility of net income, β1, is expected to be
positive. The marginal utility for an increase in carbon emissions, β2 should be negative,
at least if the average person is concerned about the negative effects of climate change.
The marginal utilities of (increases in) carbon-intensive jobs and green-industry
jobs, β3 and β4, should both be positive (assuming jobs are good). We have no priors,
however, about the signs of the coefficients on the other program attributes: β5, β6, β7,
β8 and β9. Preferences about ways in which the programs could be implemented, and
therefore the possible distributional consequences of these programs, remain an empirical
question, and these preferences may be heterogeneous within the sample.
53
Note that using intuition analogous to that for marginal WTP estimates,
equation (??) allows us to determine, for example, what percent of jobs in carbon-
intensive industries in their county people would be willing to give up to achieve a given
percent reduction in carbon emissions, holding all other program characteristics constant.
This is an elasticity-type measure. Likewise, we can use this equation to determine what
percent of jobs in carbon-intensive industries in their county people would be willing to
give up to get given percent increase in the number of green jobs in their county via a cap-
and-trade program, holding all other program attributes constant.
Finally, there is also an analog to the concept of a total willingness to pay. If we
are given the cost and effectiveness of a carbon cap-and-trade program, along with the
percent increase in green jobs that would result, as well as the five variables that define
how the program would be implemented, equation (??) can tell us what percentage of
jobs in carbon-intensive industries people would be willing to sacrifice, in that context, to
achieve a one percent decrease in carbon emissions.9
3.2.2 Heterogeneous preferences.
3.2.2.1 Mixed logit models. Mixed logit models are continuous mixture
models. The mixed logit model starts from a homogeneous-preferences specification
as in equation (3.6). However, instead of assuming that each marginal utility parameter
is a true but unknown constant, identical for everyone in the sample, the mixed logit
allows some or all of the marginal utilities to have a distribution across the population. An
explicit functional form must be selected for the assumed distribution of each parameter,
and the goal of estimation shifts to estimation of the central tendency and dispersion
of these parameters in the population. Instead of just estimating the expected value of
marginal utility, therefore, we typically estimate both the mean and the standard deviation
9A bootstrap approach, or the delta method, or Fieller’s method would likewise need to be used to
provide point and interval estimates for this percentage, since we are still dealing with ratios of utility
parameters estimated by maximum likelihood.
54
of the distribution of that marginal utilities, across the population. These distributions
accommodate “unobserved heterogeneity” in preferences. We do not seek to attribute this
heterogeneity to any specific, observable respondent characteristics. Instead, we merely
permit heterogeneity in preferences to exist.
Mixed logit probabilities are the integrals of ordinary conditional logit
probabilities, with the integrals taken over the density function for the random parameters
in the model. Suppose we begin with the conditional logit choice probabilities that
individual i will select alternative j, where we now denote this logit probability as Li j.
We now normalilze on alternative J, to permit unique estimates of the parameters β :
exp(∆V jt
L (β) = i
)
i j
1+∑J−1
(3.8)
k=1 exp(∆V
kt
i )
The mixed-logit probability that individua∫l i will select alternative j is given by:
Pi j(β) = Li j(β) f (β)dβ (3.9)
where f (β) is the density function for the parameter vector that accommodates
unobserved heterogeneity in preferences, and the observed portion of utility, V jti (which
captures at least the baseline attributes of each alternative, as featured in equation (3.1)),
is embedded in the Li j(β) term. The mixed logit probability formula can be interpreted as
a weighted average of the standard conditional logit formula evaluated at all the different
values of the parameter vector β, where the weights are given by the parameter density
function f (β), also known as the “mixing distribution.” We note that if the mixing
distribution is degenerate at a set of fixed β parameters, the mixed logit model collapses
to just the standard conditional logit model. If the mixing distibution is discrete, the
mixed logit model becomes the latent class model (i.e. a finite mixture model) described
in the next section.
Mixed logit estimation algorithms permit the user to choose among a variety of
distributions for each parameter. If the parameter vector is assumed to be multivariate
55
normal with mean vector b and covariance matrix W , then the mixed-logit choice
probabilities are given by: ∫ ( )exp jt(∆Vi )Pi j = J−1 kt φ(β |b,W )dβ (3.10)1+∑k=1 exp(∆Vi )
A log-normal distribution is sometimes chosen, however, because of its ability constrain
the sign on a parameter. Parameters can be individually noisy but independent, or they
can also be correlated across individuals in the sample. For example, people with a
higher-than-average marginal (dis)utility from losses of jobs in the carbon-intensive
sector may also derive lower-than-average marginal utility from gains of jobs in the green
sector. These could be older workers with less ability to change careers. Other people
in the sample may have a lower-than-average (dis)utility from losses of carbon jobs but
a higher-than-average marginal utility from gains in green jobs. These folks could be
younger and still flexible in their career choices. A mixed logit with correlated preference
parameters permits these more-general forms of heterogeneity in preferences while still
permitting us to estimate ‘average” preferences for use in scaling WTP estimates from a
representative sample to the entire population.
In cases where there is more than one choice per individual, there may be some
commonality among different choices by the same individual. In estimation of the mixed
logit by maximum simulated likelihood methods, it is appropriate to make one draw from
the joint distribution of the preference parameters per individual, rather than separate
draws for each choice occasion.
Mixed-logit models that allow for unobserved variation in preferences are
relatively parsimonious. For our model in equation (3.6), there are eight basic marginal
utility parameters. If we allow each of these parameters to be random but independent,
the parameter space expands to 16. If we had enough data to permit all parameters to be
random and also correlated across respondents, there would be eight parameter means and
56
eight corresponding parameter standard errors to estimate, along with the 8(8−1)/2 = 28
off-diagonals of the symmetric parameter covariance/correlation matrix to estimate.
Random parameters mixed-logit models, especially when there are repeated choices
for each respondent, can greatly improve a researcher’s ability to estimate the average
preferences in the population, controlling for unobserved heterogeneity. But mixed logit
models do not help us identify interesting systematic variation in preferences according to
observed respondent characteristics—namely observed preference heterogeneity that may
be very important to our understanding of the distributional consequences of a policy,
when we are likely to need to understand which groups of people are willing to pay more
for these programs (i.e. will derive greater benefits) and which are willing to pay less (i.e.
will derive lesser benefits).10
3.2.2.2 Latent class models. Many researchers working with choice data
now entertain latent-class models. In these models, it is assumed that respondents’
preferences are a finite mixture of a small number of underlying preference types, each
with it own vector of preference parameters, βc, for each preference class c, entering into
the expression for ∆V jti . Within preference class c, individual i’s choice probabilities are
given by:
( )
T J exp ∆V jt
yit j
(
P (β ) = ∏∏ i )i c (3.11)
t=1 j=1 1+∑J−1 ktk=1 exp(∆Vi )
These latent preferences are assumed to be homogeneous within class c, so that
only the linear-in-variables preference parameters β = (β1, ...,β9) would be estimated for
each class.
10For the preliminary results reported in this version of the paper, we use Stata’s mixlogit algorithm. For
subsequent versions of the paper, we expect to shift to the specialized choice-modeling algorithms offered
in Apollo, a software package based on the R language, offered by the Choice Modelling Centre at Leeds
University in the UK.
57
The difference from the split-sample model in equation (??), however, is that
we do not observe class membership. Instead, preference class membership is only
probabilistic. These distinct sets of preference parameters are subsumed in a model that
also employs a class membership equation. The respondent’s latent class membership
probability depends not on the attributes of the different cap-and-trade programs, but
exclusively on the individual or neighborhood characteristics of the respondent. Let si
be a vector of such (typically sociodemographic) characteristics for respondent i or the
population in their geographic area (e.g. ZIP code, county, etc.).
These respondent characteristics do not differ across alternatives in the program
choice tasks, so the class-membership part of the model takes the form of a so-called
multinomial logit model, where the probability of belonging to a particular class involves
a different set of multinomial logit coefficients for each class (and the coefficients
are normalized to zero for an arbitrarily designated numeraire class). The same set of
respondent characteristics leads to different probabilities of belonging to each preference
class only because the coefficients that multiply these characteristics differ across
classes. Thus if there are C different preference classes, there will be C − 1 sets of
coefficients on the vector of respondent or neighborhood characteristics that determine
the probabilities of class membership. Then, conditional on class membership, the model
embeds a conventional conditional-logit-type choice model for each class that involves
homogeneous preferences within that class.
The the probability that individual i belongs to preference class c is given by the
multinomial logit probability:
exp(s
π i
θc)
ic(θc) =
1+∑C−1
(3.12)
l=1 exp(siθl)
where the vector si typically includes a constant term and θc is a conformable vector
of class-membership model coefficients for class c, with θC normalized to 0 for
58
identification (i.e. so that the θ vectors are uniquely estimated). The full set of class
membership coefficients is then Θ = (θ1, ...θC−1). For the full latent class model, the
joint likelihood of individual i’s choice will then be:11
C
L (B,Θ) = ∑ πic(θc)Pi(βc) (3.13)
c=1
Latent class models can be somewhat balky to estimate when there are many
respondent characteristics to consider. Suppose there are k1 individual or neighborhood
characteristics for respondents, k2 carbon cap-and-trade program attributes, and C latent
classes are being entertained. Then the parameter space for the model will be on the
order of (C − 1)× k1 +C × k2. The greatest success generally comes from starting
with an extremely parsimonious specification and gradually adding more respondent
characteristics (implicitly freeing up their coefficients to be non-zero). For each additional
program attribute, C additional parameters are added to the model. For each additional
respondent characteristic, C − 1 additional coefficients are added. For each additional
class of preferences, k1 + k2 more parameters must be estimated.12
3.2.2.3 Preferences that vary systematically with observable respondent
characteristics. When the researcher has a wealth of information about respondent
characteristics, it is possible to estimate models where each marginal utility parameter in
the choice model is permitted to vary systematically as a function of these characteristics,
as indicated by the data. We reserve for future extensions of this paper a set of
specifications that accommodate this “observable” preference heterogeneity via
interaction terms between program attributes and respondent characteristics, as selected
11For repeated choices by the same individual, the model can be estimated to allow for commonalities in
choices within an individual.
12For the results presented in this version of the paper, we use Stata’s lclogit2 algorithm to search for a
set of parameter estimates that brings us close to the maximum likelihood solution but does not produce a
parameter variance-covariance matrix. These estimates are then used as starting values for the follow-on
algorithm, lclogitml2, to attain the maximum likelihood solution and produce the parameter variance-
covariance matrix needed for hypothesis testing and for the calculation of WTP estimates. In future versions
of the paper, we expect to use Apollo’s R-based altorithms.
59
by LASSO methods. Specifications such as these can be very useful in helping to
establish the so-called construct validity of the preference estimates. If marginal utilities
vary in ways one would expect across people with different characteristics, these
relationships add credence to the empirical results.
3.3 Outline of Survey and Data
3.3.1 Sketch of the survey instrument. Our survey was initially drafted
in the lead-up to the consideration of Oregon House Bill 2020 in the winter of 2019, but
the state legislature’s vote on that bill never took place because the Republican house
members left the state to prevent the Democratic members from reaching a quorum. Thus
we shelved the project for several months until Oregon Senate Bill 1530 was proposed for
the 2020 session, when the same exodus of Republican representatives occurred. After
the 2020 legislative session concluded, however, Oregon experienced the worst wildfire
season in years, and significant drought conditions continue. We resolved to redesign the
cap-and-trade survey and use it to try to determine which features of a potential cap-and-
trade program might account for heterogeneity in support. Casual empiricism suggests
that attitudes toward climate change are determined predominantly by partisanship. The
goal of our survey, therefore, is to explain some of the options for cap-and-trade program
design and to learn whether support for cap-and-trade programs in Oregon varies only
with political ideology, or whether there is evidence of systematic differences in support
as a function of program attributes, other individual characteristics, or neighborhood
characteristics for the respondent.
The survey was developed during the winter and spring of 2021, and the full
launch commenced on August 5, 2021. Quota sampling was used to produce an sample of
completed responses for which the marginal distributions of age (over 18), gender, race,
and household income are consistent with the marginal distributions for these variables in
the population of Oregon.
60
The structure of our survey is described in detail in Appendix B.2. One instance of
the randomized survey instrument, as it would be viewed by a respondent, is included as
Appendix B.3.
3.3.2 Sample Selection. One challenge in using data based on a voluntary
survey is the distinct possibility of sample selection bias. If characteristics that determine
an individual’s propensity to complete the survey also systematically affect their WTP
for these program, then the WTP estimates from a naive model risk being biased. For
instance, if people who work in the logging industry are less likely to complete our survey
and have a lower WTP for carbon emission reduction then we will tend to overestimate
WTP for carbon emission reductions in the general population of the state. On the
other hand, if people in higher income brackets have higher marginal values of their
time and are thus less likely to take the survey, and these higher-income people are also
more willing to pay the costs of a carbon cap-and-trade program , then we will tend
to underestimate the WTP in the general population. Given the highly politicized and
socially polarizing nature of climate change policies we are acutely aware of the necessity
of evaluating our data for sample bias, and to correct for this bias if it exists.
To address sample selection, we leverage a set of “screening” sociodemographic
variables elicited from all survey invitees, including those who drop out after learning
the survey’s topic. These variables include self-reported age, gender, race, and income
bracket, as well as the potential respondent’s ZIP code of residence). Based on the ZIP
code information for the respondent’s neighborhood (we asked respondents to report their
neighborhood ZIP code if they collected their mail from a PO Box), we merge in a host of
external information that can be geographically indexed to ZIP codes or their centroids.13
13Additionally, a handful of other survey response variables are know for all respondents (e.g. day survey
was taken and if the survey was taken on a mobile device).
61
The external data sets we employed to create profiles of each respondent’s
neighborhood include: the American Community Survey 5-year ZCTA-level data
(2014-2019), the MIT Election Data and Science Lab’s County Presidential Election
Returns (2020), Oregon State Office Returns for 2016 state legislative district votes
(by major party), drought data from National Drought Mitigation Center, and wildfire
data from Wildland Fire Decision Support System. We create population proportion
sociodemographics (e.g. share of the population for each ZIP code that has access to the
internet) as well as a number of climate-related statistics for each zip code (e.g. Drought
Monitor rating, or distance to the nearest wildfire in 2020). The zip-code-level profiles
are constructed to capture political ideologies, salience of climate change, and other
sociodemographics that we hypothesize may impact each potential respondent’s prpensity
to continue with the survey, to completion, after learning its topic.
We use a probit model to estimate each eligible potential respondent’s propensity
to complete the survey. We then allow the fitted propensity to shift all of our estimated
preference parameters. This ad hoc correction approach allows us to simulate, counter-
factually, what would have been the marginal utility from each program attribute had
everyone in the estimating sample been equally as likely to complete the survey as the
average for all eligible respondents.
It should be noted that while we correct for sample selection in terms of the
willingness of individuals to complete a carbon cap-and-trade survey, another potential
type of sample selection remains unavoidable: people who are willing to take an (internet)
survey upon an invitation from Qualtrics may not be representative of the general
population. While this other form of sample selection is perhaps of lesser concern, it
exists nonetheless and is difficult to address.
62
3.4 Results and Discussion
3.4.1 Sample Selection. One challenge in using data based on a voluntary
survey is the risk of sample selection bias. If characteristics that determine an individual’s
propensity to complete the survey also systematically affect their WTP for these
programs, then the WTP estimates from a naive model may be biased. For example,
people who work in the logging industry might be less likely to respond to our survey
and have a lower WTP for carbon emission reductions. Basing our estimates strictly on
respondent preferences, we might tend overestimate WTP for carbon emission reductions
in the general population of the state. Another possibility might be that people in higher
income brackets have higher marginal values of their time and are thus less likely to
complete the survey. If these higher-income people are also more willing to pay the costs
of a carbon cap-and-trade program, then we might tend to underestimate the WTP in the
general population. Given the highly politicized and socially polarizing nature of climate
change policies we are acutely aware of the necessity of evaluating our data for sample
bias, and to seek to correct for this bias if it exists.
To address sample selection, we leverage a set of “screening” sociodemographic
variables available for all survey invitees, including those who drop out after learning
the survey’s topic. These variables include self-reported age, gender, race, and income
bracket, as well as the potential respondent’s ZIP code of residence). Based on the ZIP
code information for the respondent’s neighborhood (we ask respondents to report their
neighborhood ZIP code if they collect their mail from a PO Box), we merge in a host
of external information that can be geographically indexed to ZIP code polygons or
centroids.14 We explicitly model the propensity for an invited respondent to complete
the survey. Ideally, each person would be equally likely to respond, so we take the mean
14Additionally, a handful of automatically collected survey-context variables are known for all
respondents (e.g. the date and time when survey was accessed and whether the survey was taken on a
mobile device).
63
predicted response propensity in the invited group and subtract this from the predicted
response propensities of everyone in the respondent sample, creating a variable that would
be zero if everyone in the estimating sample were equally likely to complete the survey.
In our models, we allow for interactions between this demeaned response propensity,
denoted dm : R̂P, and every program attribute. We then counterfactually simulate
what would be the predicted marginal utilities for each program attribute if everyone
had a response propensity equal to the mean among all invited participants (i.e., had
dm : R̂P = 0). We use these corrected marginal utilities in calculating the implications of
our estimates. For details about our response propensity model, please see Appendix B.4
in the online Supplementary Materials.
3.4.2 Program choice model: Homogeneous preferences. Our choice
experiments involve binary choices between one cap-and-trade program and the status
quo. Each of our six cap-and-trade programs is described in terms of a common set of
attributes. The cost of the program is in dollars per household per month. The benefit
from the program is the percentage change in carbon emissions to be achieved with the
program (always negative). Other attributes of the program include its consequences in
terms of jobs in the respondent’s own (named) county: the expected percentage-point
change in carbon-intensive industry jobs (always negative), and the expected percentage-
point change in green industry jobs (always positive). Other program attributes include
the percentage share of carbon permits that will be auctioned, and for permit auction
revenues, the percentage share that will be spent on equipment and machinery that will
help households and industries adapt to a lower-carbon economy, and the percentage
share that will be spent to help workers and communities adapt to the new conditions.
The remaining percentage share of revenues (the omitted numeraire share) will be added
to Oregon’s General Fund and used to replace other existing tax revenues. The final
attribute of each program is an indicator for whether there will be new regulations on
64
co-pollutants to prevent firm that purchase carbon permits from simultaneously increasing
their local emissions of conventional pollutants that are not globally uniformly mixing.15
We consolidate the descriptive statistics for all variables used in the different
models in this paper into Tables 9 and ??. Panel 1 of Table 9 provides descriptive
statistics for the different cap-and-trade programs offered to respondents; each respondent
sees a different set of six randomly generated programs, called A through F. Our sample
of 6300 programs reflects six program choices for each of 1050 respondents.
Inferences derived from choice experiments can sometimes be sensitive to
the specification of the choice model and its assumed stochastic structure. All of our
specifications focus on the nine β parameters appearing in equation (3.6), but we
will report estimates of these marginal utilities from a set of five different estimating
specifications:
1. A simple linear-in-parameters conditional logit choice model that assumes
homogeneous preferences but allows a respondent’s predicted survey response
propensity to shift one of the marginal utilities;
2. A mixed logit model where the marginal utilities for attributes other than program
cost are allowed to vary randomly but independently across respondents;
3. A latent class model with two classes where class membership is allowed to vary
systematically with a number of respondent characteristics;
4. An alternative latent class model with two classes where (endogenous) political
ideologies and attitudes toward climate change influence class membership;
5. A streamlined model where LASSO methods have been employed to select
important dimensions of systematic heterogeneity in marginal utilities across a
selection of county-level contextual variables for each respondent. This model can
be employed, cautiously, for “benefits transfer” exercises to extend the inferences
from our study to states other than Oregon.
For ease of comparing our estimates of the β parameters across specifications, we use
Table 11 to report just these basic utility parameters for all five models (along with the
15See Appendix B.5 for details on how the choice sets were generated for our cap-and-trade program
alternatives.
65
log-likelihood value and counts of respondents, programs, and alternatives). For Model
1, of course, these are the only parameters to be estimated. For models 2, 3, 4, and 5,
however, we provide Tables 12, 13, 14 and 15, each reporting the additional parameters
unique to that specification (beyond just the basic marginal utility coefficients).
Our simplest program choice specification is a straightforward conditional logit
model with homogeneous preferences, shown as Model (1) in Table 11. The respondent’s
choice between the program being offered and “No Program” depends on all of the
program attributes as well as the usual “Status quo” indicator variable. The coefficient
on “Status quo” conveys the extent to which respondents are systematically more or less
likely to choose “No Program” regardless of the attributes of the particular cap-and-trade
program they are being offered.16 Model (1) suggests that all program attributes other
than those related to the auctioning of permits and the use of the resulting revenues have
non-zero marginal utilities. Higher program costs are undesirable, as are higher carbon
emissions, but respondents, on average, derive positive utility from any cap-and-trade
program to reduce carbon emissions, regardless of its specific attributes. More jobs are
desirable, whether they are carbon jobs or green jobs, as are new regulations on other
pollutants. However, the restrictions implicitly embodied in this model are rejected by our
richer specifications.
We note, however, that Model (1) in Table 11 shows that our ad hoc selection
correction term, (dm : R̂Pi), has a statistically significant effect on the estimated marginal
utility from a proportional change in green jobs in the respondent’s county.17 After
16For ease of interpretation, it will sometimes be convenient to convert this, ex post, to an “Any program”
indicator by multiplying both the indicator and its coefficient by -1.
17An uncorrected model, as well as a model with dm : R̂Pi permitted to shift all of the marginal utility
parameters, are explored in Stanford and Cameron (2022). Model (1) involves eight parameter restrictions
relative to the fully interacted model, but the maximized log-likelihood for the more-general model
increases by only about three points, suggesting that the restrictions embodied in Model (1) reported here
cannot be rejected.
66
selection correction, the baseline coefficient on marginal utility for green jobs increases in
magnitude and remains positive and statistically significant at the 5% level. The negative
coefficient on the interaction term between the green jobs attribute and the demeaned
selection propensity indicates that the more likely a respondent is to participate in the
survey, the lower their marginal utility from an increase in green jobs.18
3.4.3 Program choices: Heterogeneous preferences.
3.4.3.1 Unobserved heterogeneity: Mixed logit specifications. As noted
in Section 2, heterogeneous preferences can be modeled in a variety of ways in the
analysis of choices. If the researcher has no information beyond just the attributes of
the alternatives and respondent’s preferred option in each choice task, the most common
way to accommodate heterogeneity in preferences is to explore mixed logit models (i.e.,
models with random parameters, where each member of the population is assumed
to have different marginal utilities for each attribute, and these marginal utilities have
specific parametric distributions). A common exception is the cost variable. Benefit-cost
analyses in the U.S. typically assume that everyone shares the identical marginal utility
of income, which would imply a common marginal disutility of program cost. We follow
the convention of constraining the coefficient on the cost variable to be a fixed parameter,
rather than a random parameter. But we let all of the other coefficients in our basic model
have normal distributions, and we estimate both means and standard deviations for these
parameter distributions.
Model 2 in Table 11 allows each marginal utility other than that for the cost
variable to be independently normally distributed. In shifting to this model, the mean
values of these marginal utilities for most program features increase in magnitude and in
18The sign of this coefficient runs counter to our initial expectation. We anticipated that people who
are more concerned about climate change and more optimistic about green jobs would be more likely to
complete our survey, but it seems that responses were also more likely from people who see climate policy,
and especially the shift to green jobs, as a threat to their well-being.
67
some cases in significance, but the fixed estimate for the cost coefficient also increases,
so the net effects on our eventual willingness-to-pay calculations will be smaller. Among
the more fragile coefficients on the auction-related attributes, the mean marginal utilities
for the share of permits auctioned changes sign but remains statistically insignificant.
The marginal utility for the shares of auction revenues going to workers/communities
becomes significant at the 5% level. If auction revenue is generated by a given cap-and-
trade program, there is thus some suggestion that respondents may approve of revenue
recycling directed towards workers and communities. The point estimates suggest that
revenue recycling toward businesses, for updating of equipment and machinery, may be
viewed less favorably.
The mean marginal utilities for Model (2) differ somewhat from the fixed marginal
utilities for Model (1) because Model (2) also estimates standard deviations for these
marginal utilities across the sample of respondents. Table 12 gives Model (2)’s additional
point estimates and standard errors for these marginal utility standard deviations. The
standard deviations of the marginal utilities for several attributes—i.e., “Any program,”
carbon emissions, carbon jobs, the share of auction revenues going to workers, and
the presence of new regulations on other pollutants—are all statistically significantly
different from zero, pointing to discernible heterogeneity in preferences concerning those
attributes.19
3.4.3.2 Latent class models. For each of our two different latent class
models, only two classes of preferences can be reliably distinguished. Each respondent’s
19Stanford and Cameron (2022) also reports a specification where these marginal utilities (other than that
for the cost attribute) are also allowed to be correlated across respondents. Some of these 28 correlations
are statistically significant. For example, the marginal utilities for the two types of jobs are positively
correlated, suggesting that people either care about jobs in general, or do not care as much about jobs. The
marginal utility for regulations on other pollutants is positively correlated with the marginal utility from
the status quo, suggesting perhaps that climate skeptics do not want a cap-and-trade program, but they may
still be concerned about other types of pollution. However, a likelihood ratio test for all 28 of the additional
parameter correlations does not reject the model where parameters are independently distributed, so we
report only the model with independently distributed random parameters here.
68
characteristics are permitted to explain latent class membership in one submodel that has
the structure of a multinomial logit model, and one set of marginal utility parameters for
program attributes is estimated for each class of preferences, with these two submodels
each having a structure analogous to a conditional logit model.
Our first latent class specification, Model (3), allows class membership to be
determined by the set of respondent characteristics with descriptive statistics shown
in section 2 of Table ??. The two sets of preference parameters are displayed in
Table 11, and the coefficient estimates for the single-index class membership model
are shown in auxiliary Table 13. Class membership is a function of broad bins for
several sociodemographic characteristics: educational attainment, income, gender, age,
parenthood status, awareness of forebearers,20 and past and expected future duration of
residence in Oregon.
In the two discernible classes of preferences, the positive baseline marginal utility
associated with “Any program” shows that Class 1 preferences are generally in favor of
cap-and-trade programs, regardless of their attributes, and Class 2 preferences tend to
oppose any of these programs. Both preference classes care about the proportional change
in carbon emissions (Class 2 somewhat more so). Both classes care about carbon jobs
in Model 3, but only Class 1 cares about carbon jobs in Model (4). Class 1 cares about
green jobs in both models, but Class 2 does not care about green jobs in either model.
The coefficient for the selection correction term also bears a different sign across these
two groups. Given that there is no separately estimated scale factor (error variance) for
one of the two sets of preferences, we should be able to compare the marginal utilities
for each class. Beyond the sign difference for the “Any program” and selection effects,
however, it is not particularly intuitive to compare the two sets of preferences because
20We included our questions about forebearers and descendants to permit hypothesis testing about
whether someone who feels a greater degree of connection to past (i.e. inter-generational awareness) may
feel more obligated to support policies that will reduce climate change damages for future generations.
69
they do not share the same estimated marginal utility of income (implied by the negative
of the marginal (dis)utility of the cost attribute). In a later section, where we discuss the
implications of our estimated models, we report comparable estimates of the trade-offs
people willingly make, as implied by different preferences, for all our different models, so
we postpone discussion of these implications until then.
Model 4 in Table 11 also allows two latent classes of preferences, but explores
how class membership is related to four sets of indicators variables that classify
respondent’s political ideologies and attitudes about climate change. Section 3 of
Table ?? gives descriptive statistics for the proportions of the sample that identify with the
Democratic Party or the Republican Party (where the omitted category is "Independent
or other"). The next dimension is whether their political ideology is “liberal” or “very
liberal” or “conservative” or “very conservative” (relative to the omitted category of
“moderate”). The next set draws from respondents’ answers on a five-point Likert
scale concerning whether climate change is real and is a serious threat. Finally, we
use answers to a Likert-scale question about whether climate change is human-caused
(where we combine the two “disagrees” categories due to low numbers). We chose these
four dimensions of political ideology or attitudes about climate change because casual
empiricism suggests that these factors have been extremely important with respect to
Oregon’s recent experience with legislation concerning potential carbon cap-and-trade
programs.
The marginal utility parameters for the two latent classes of preferences in
Model (4) are given in Table 11. The negative status quo effect reveals that Class 1
finds cap-and-trade programs to be desirable in general, whereas Class 2 is more likely
to choose “No program,” regardless of the levels of the program’s other attributes.
Class 1, in this case, cares about both carbon jobs and green jobs, whereas Class 2
is not particularly concerned about either kind of jobs (these marginal utilities are
70
not statistically significantly different from zero for Class 2). However, there is some
evidence from this specification to suggest that both groups view revenue recycling
directed to workers as desirable, although both classes are statistically indifferent to the
share of permits being auctioned.
We explore four different sets of indicator variables that capture a respondent’s
political ideology and attitude towards climate change. In Stanford and Cameron (2022),
we rotate through these four sets of variables and find that all four sets, individually, have
strongly significant effects on class membership. In model (4) of Table 11, we include all
four sets of ideological and climate-change attitude variables in the same specification,
to determine whether one type of variable dominates when we control for the others.
The most statistically significant of the four sets of factors is whether the respondent
agrees or strongly agrees that climate change is real, human-caused and is a significant
threat. The negative coefficients on these indicators imply that these respondents are
more likely to belong to Class 2. Climate attitudes are clearly a very strong driver of
preferences for cap-and-trade programs. One interesting result is that if we use only the
party affiliation indicators (e.g. Democrat, Republican, from results reported in Stanford
and Cameron (2022)), Republicans are less enthusiastic about cap-and-trade programs
than non-Republicans. However, when we control for attitudes about climate change (the
level of threat it presents, and whether it is human-caused), Republican respondents are
actually more likely to support cap-and-trade programs.
3.4.4 Program choices: Observable heterogeneity and benefits transfer.
Our survey sample was limited to the state of Oregon.21 Oregon is sometimes perceived
to be a very liberal state, but there is great variation in sociodemographics and political
ideologies across urbanized and rural counties in the state. We estimate Model 5 in
Table 11 as a choice model with observed heterogeneity as a function only of census ZIP
21This was an artifact of our funding sources.
71
code tabulation area (ZCTA)level characteristics for each respondent. We allow the best
set of predictive ZCTA characteristics within the Oregon estimating sample to be selected
by LASSO methods. If the variability across Oregon ZCTAs is sufficient, compared to the
variability across all ZCTAs in the lower-48 U.S. states, it may be safe to transfer a model
fitted for Oregon ZCTAs to all ZCTAs in other states.
Table 10 reports a LASSO-selected set of ZCTA-level characteristics that capture
preferences for cap-and-trade policies. We report the means and standard deviations of
these ZCTA proportions associated with each respondent in our sample, along with the
same ZCTA-level characteristics for the 430 ZCTAs in Oregon, and then for all 33,300
ZCTAs across the lower-48 states of the U.S.22
For Model 5, shown in the last column of Table 11, Table 15 shows the interaction
terms that survive the LASSO variable-selection process. The greatest number of
dimensions of heterogeneity is evident for the marginal utility from Any Program,
independent of the program’s attributes. Neighborhood characteristics that account for
a statistically significant increase in a respondent’s utility from any program include
the proportion of their ZCTA that: is multiracial (of two or more races), is divorced
or separated, has a bachelor’s degree, has income between $15,000 and $25,000, is a
native U.S. citizen but born outside the US, is employed in the utilities industry, uses
a smartphone to access the internet, or commutes by “other means.” Utility from “Any
Program” is statistically significant lower, the greater the proportion of the respondent’s
ZCTA that: has income of $10,000 or less, or income of $65,000 to $75,000, accesses the
internet via a tablet or portable wireless device, heats their home with fuel oil, kerosene,
or similar, or has one or two vehicles available for commuting.
22ZCTAs within a handful of relatively liberal urban counties, many in the northern part of the Oregon,
contain much of the population, and most of the eastern counties are very sparsely populated and relatively
conservative. It is worth noting that factions in the eastern part of Oregon have occasionally lobbied to join
Idaho, rather than stay with the rest of Oregon.
72
Table 15 also shows that the marginal (dis)utility from higher carbon emissions
is more-negative for someone in a ZCTA with a higher proportion of the population with
commuting times of 60 minutes or more (typically people living in suburban areas), and
less negative, the higher the proportion of people commuting 10 minutes or less.
Protection of carbon jobs is more important in ZCTAs with higher proportions of
people employed in wholesale trade, whereas increases in green jobs are more important
where higher proportions of people are employed in real estate, renting, or leasing (more
likely in urban/suburban areas).
On average, according to Models 1 through 4, the share of permits auctioned
does not have a statistically significant effect on the utility people derive from a carbon
cap-and-trade program. However, Table 15 reveals that enthusiasm for the auctioning
of permits is statistically significantly greater for respondents who live in ZCTAs with
higher proportions of: Native Hawaiian or Pacific Islanders, dial-up-only internet access,
or people who commute via public transportation (excluding taxis). Enthusiasm for
auctioned permits is less for respondents who live in ZCTAs with higher proportions of:
Asians, or people who heat their homes using “Other fuel” or “No fuel”.
As to the use of any auction revenues for replacing equipment, there is less
support for respondents from ZCTAs with higher proportions of people who speak some
other language at home, but still speak English well, and higher proportions of people
who are employed in Public Administration. Support for using auction revenues to help
workers and communities adjust to higher carbon prices is greater when a ZCTA has a
higher proportion of people employed in the Utilities industry, but less when a ZCTA has
more people who use “No fuel” for heating.
On average, respondents prefer programs that include new regulations on other
pollutants. Table 15 shows that this support is lower, however, the greater the proportion
of the respondent’s ZCTA that is American Indian or Alaska Native. However, support
73
for programs with new regulations is stronger, the higher the proportion of people in the
respondent’s ZCTA who rely only on a computer for internet access.
3.4.5 Implications of estimated models. Due to the estimated differences
in the marginal utility of income across the two classes in our latent class models, our
estimated utility parameters under different model specifications can be less intuitive
to compare than the estimates they can be used to produce for a number of valuation
measures for different types of cap-and-trade programs. Table 16 collects a number
of results based on some key ratios of marginal utility parameters calculated using the
distributions of the estimated parameters in each of our five models.23
We begin with our different models’ implied point estimate of the social benefits
from a reduction of one ton of carbon emissions (SBC). These numbers can, in principle,
be compared to measures in the literature for the social cost of carbon (SCC). Our
marginal utilities for proportion carbon reductions must be converted to the implied
per-ton basis. Thus our SBC estimates, for Oregon, start with our estimated marginal
willingness to pay (MWTP) carbon reductions. Respondents were shown graphics during
the survey that conveyed that the approximate aggregate annual carbon emissions for
Oregon at present is about 64 million metric tons, so total carbon emissions per month
average about 5,333,333 tons. A 1.0 proportional change in these emissions would thus
be about 5,333,333 tons per month. The total number of households in Oregon is about
1,649,000. Thus whatever estimate we get for the MWT Pemissions needs to be multiplied
by 1,649,0005,333,333 to yield the aggregate willingness to pay by Oregon households to have
Oregon’s carbon emissions reduced by 1 metric ton.
According to Model 1 in Table 16, with homogeneous preferences, this SBC
estimate is about $47/ton of carbon. Model (2) implies $61. For our two latent-class
23We rely on the wtp.ado code in Stata, developed by Hole (2007), to calculate point and interval
estimates for these ratios, with standard errors calculated using the delta method.
74
models, Class 1 preferences imply an SBC of either $64 or $56, and Class 2 preferences
imply only $35 or $28. For Model (5), where preferences are allowed to depend on
county-level characteristics, the SBC for a given county depends on anything which
systematically affects the estimated marginal utility of carbon emissions. In Model (5),
this utility is affected by the proportion of people who commute less than 10 minutes,
or more than 60 minutes (and possibly with access to broadband satellite internet). For
Model (5), we estimate the model using demeaned values of all of the interaction terms,
so that where these interaction terms are all zero, we obtain an estimate of the SBC “at the
means of the data.” This estimate is $49.
A second measure of interest for each model, in the second row of Table 16, is
a point estimate of the marginal rate of substitution (MRS) between carbon jobs and
green jobs. This measure involves the estimated coefficients on the proportional change in
carbon jobs and the proportional change in green jobs, in the respondent’s own county, as
a result of these cap-and-trade programs. The ratio of the two coefficient is:
βProp change in carbon jobs ∂ (Green jobs)/Green jobs
= (3.14)
βProp change in green jobs [∂ (Carbon jobs)/C]a[rbon jobs ]
∂ (Green jobs) Carbon jobs
=
∂ (Carbon jobs) Green jobs
so that the MRS (i.e., the number of green jobs willingly sacrificed to keep one carbon
job):
∂ (Green jobs)
MRS(Carbon jobs, Green jobs) = (3.15)
[∂ (Carbon jobs) ][ ]
βProp change in carbon jobs Green jobs
=
βProp change in green jobs Carbon jobs
If we wish to know how many green jobs people would require, on average, to make up
for the loss of one carbon job, we would use the negative of this MRS. The ratio of the
two coefficients is constant, but the MRS also depends on the ratio of green jobs to carbon
75
jobs. Thus we cannot quote a specific willingness to be compensated by green jobs for
lost carbon jobs without specifying the prevailing ratio of these two types of jobs.24 As a
representative ratio of green jobs to carbon jobs, we use the state-level ratio, and report a
point estimate and a confidence interval for this representative MRS.25
For our models with homogeneous preferences, our estimates suggest that on
average, people need about 1.27 to 1.72 green jobs to make up for each carbon job lost
due to a cap-and-trade policy. However, our two latent class models reveal very different
implications across the two preference classes. In each case, the relatively “pro-cap-and-
trade” preference class would be satisfied, on average with only about one new green
job for each carbon job lost. From Model 3, we know that Class 1 membership is more
likely for younger people who are college graduates, males, and people who expect to
stay in the state for at least two more decades. These groups may be more confident that
they would be able to retool for a career in a green job, rather than a carbon sector job.
Preference Class 2, however, the anti-cap-and-trade class, would demand about 2.2 to 6.8
new green jobs to make up for each carbon job lost. These people are more likely not to
be college graduates, to be female, to be older, and to expect to reside in Oregon for less
than 20 more years.26
The remaining rows in Table 16 report, for each of our models, the calculated
marginal willingness to pay (MWTP) per month for a program with one more unit of
each attribute, along with a confidence interval. For attributes described as proportions
24In general, the MRS will be smaller when there are relatively more carbon jobs and fewer green jobs. It
will be larger when there are relatively fewer carbon jobs and more green jobs.
25Stata’s wtp.ado algorithm can be adapted to calculate point and interval estimates for this ratio.
26The statistically significant but negative effect on Class 1 membership of knowing one’s ancestors
beyond great-great-grandparents may seem counter-intuitive. We had been curious about whether people
who pay attention to their family history might have been more likely to care about what their descendants
think of their position on climate change policies. Instead, it may simply be the case that older people are
more likely to be interested in genealogy than younger people, but younger people feel greater urgency
about limiting climate change.
76
or shares, these marginal WTP amounts are for a 1.00 or 100% proportional change, or
for a 1.00 or 100% change in share. The reported marginal WTP amounts could be scaled
to a 1% change in jobs, or a 1% change in share by dividing the MWTP estimate (and its
confidence bounds) by 100.
First, consider the baseline WTP for any type of cap and trade program, regardless
of its attributes. This MWTP implied by the coefficient on the “Any Program” indicator.
For Models (1) and (2), the estimated (mean) preferences suggest a positive WTP for any
program, although this baseline positive WTP could be offset by too-small reductions in
carbon emissions or too-great losses of carbon jobs. Each of our two latent-class models,
however, reveal very different baseline WTP amounts for cap-and-trade programs across
the two preference classes. In both latent class models, Class 1 has a baseline WTP
for a cap-and-trade program on the order of about $253-$284. Class 2, however, has a
negative baseline WTP, on the order of -$75 to -$107. This baseline, however, could also
be overcome by a sufficiently large reduction in carbon emissions, a sufficiently small
loss of carbon jobs, and/or a sufficiently large increase in green jobs, augmented by new
regulations on other pollutants.
Second, the distributional effects of alternative cap-and-trade programs will be felt
partly through their effects on employment in different sectors. Models (1), (2), and (5),
with single estimates of this measure, imply that proportional changes in carbon-sector
jobs are valued more highly than proportional changes in green jobs. However, the
two latent-class specifications reveal that the pro-cap-and-trade Class 1 preferences
are willing to pay much more for jobs of either type than are Class 2 preferences. The
difference for Class 2 preferences in Model 4 is particularly striking. Class 2 membership
is dominated by people who do not think climate change is a threat, or that it is human-
caused. Controlling for those attitudes about climate change, they also tend not to be
Republicans. This preference class has a marginal willingness to pay for proportional
77
changes in carbon jobs of only $154, and for green jobs of only $79. The corresponding
MWTP estimates for Class 1 in Model (4) are $527 and $589! Clearly, social justice in
terms of the distribution of employment impacts is vastly more important to Class 1 than
Class 2, according to Model (4).
Finally, the MWTP for cap-and-trade policies that include new regulations
on other pollutants is positive for all our models. Distributional effects of climate
policies may also depend on the extent to which transactions involving carbon permits
move production around spatially. If increases in carbon emissions are correlated with
increases in other types of pollution, residents in the vicinity of plants that buy carbon
permits could be at a disadvantage. Models (1), (2), and (5), and Class 1 preferences in
both our latent class specification, imply that programs with new regulations on other
pollutants are valued about $53 to $62 higher per month than for programs without this
feature. Many people care about the environmental justice implications of cap-and-trade
programs. For Class 2 in both of our latent class models, however, marginal WTP for
a program with new regulations on other pollutants is lower, at about half the size ($29
to $35 only). MWTP for this feature is still positive for Class 2, but this group appears
to be less concerned about the environmental justice implications of any cap-and-trade
program.
3.4.5.1 Benefit function transfer to all ZCTAs in the lower-48 U.S. states.
To accomplish this crude benefits transfer exercise, we need to assume that our fitted
preference parameters (from our Model (5) with observable heterogeneity at the
respondent’s ZCTA level), employed with ZCTA-level characteristics for any other ZCTA
in the U.S. can predict an approximate willingness to pay for a cap-and-trade program
with specific characteristics for a representative household in that ZCTA.
We could consider any cap-and-trade program that could be described by levels
of the attributes we include in our study. For simplicity, however, we will calculate
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the representative total WTP for each ZCTA in the lower-48 U.S. states for just two
programs: (a) a "basic" program that reduces carbon emissions by 40 percent but
(artificially) involves no change in the numbers of carbon jobs or green jobs, and (b)
and “alternative” program, also with a 40 percent carbon emissions reductions, but
with an arbitrary 10% decrease in county-level carbon jobs, a 10% increase in county-
level green jobs, 50% of carbon permits auctioned, with 30% of auction revenues going
towards equipment (re-tooling) and 30% of auction revenue going to help workers and
communities, and with new regulations on other pollutants.
Our first "basic" program auctions no permits, so the shares of revenue for
equipment or for workers are also zero, and no new regulations for other pollutants
are involved. By setting to zero all the other attributes, we can focus on ZCTA-level
estimates of a representative ZCTA resident’s willingness to pay for a 40 percent carbon
reduction by cap-and-trade before factoring in the (distributional) effects of the program
on carbon jobs and green jobs, or different attitudes towards auctioning of permits
and revenue recycling (another distributional issue) or the need for new regulations to
limit other pollutants (also a distributional concern). For this benefit-function transfer
exercise, the only heterogeneity in Model (5) that will matter is the heterogeneity in the
marginal utility from “Any Program” and the heterogeneity in the marginal utility from a
proportional change in carbon emissions.
3.4.5.2 Distribution of WTP for cap-and-trade programs across ZCTAs.
Our benefit-function transfer process yields a distribution of 33,300 different predicted
median WTP amounts–one for each ZCTA in the lower-48 U.S. states. The heterogeneity
in preferences identified by our LASSO variable selection is considerable. To illustrate
this heterogeneity, we provide just one examples of the differing marginal distributions
of WTP for our “basic” and “alternative” cap-and-trade programs. We split the 33,300
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ZCTAs by terciles of one ZCTA characteristics (here, the proportion of the population
commuting by public transit, not including taxis).
We display the marginal distribution of median WTP amounts for each tercile
(11,100 ZCTAs each) and mention the median WTP for each tercile in the legend to
the densities. We show the overall national median WTP (after weighting by ZCTA
populations) below each combined density plot. For our “basic” program, these ZCTA
public transit tercile distributions are shown in Figure 3. Across all ZCTAs in the lower-
48 states, the population-weighted median WTP for the basic program is $70. Median
WTP for the lower tercile of public transit use is $26, while for the upper tercile, it is
$145. Furthermore, within each tercile, there is extensive heterogeneity in WTP for the
basic program, due to other characteristics of each ZCTA. Only 0.64% of the 33,300
ZCTAs have predicted WTP for this basic program greater than $800.27
For our “alternative” program, analogous ZCTA public transit tercile distributions
are shown in Figure 4. Across all ZCTAs in the lower-48 states, the population-weighted
median WTP for this alternative program is larger, at $114. Median WTP amounts for
each tercile now decline with increasing terciles of public transit use (from $150 to $116
to $70), rather than increasing across terciles, as in the case of the basic program. WTP
for this alternative program is sufficiently higher that 5.06% of ZCTAs have predicted
WTP amounts in excess of $800.28
3.4.5.3 Spatial heterogeneity in WTP for different cap-and-trade programs.
To visualize the spatial heterogeneity in WTP to reduce carbon emissions by cap-and-
trade (distinct from any distributional consequences of such a program), we can apply
27Outlier amounts for predicted WTP are due to outlier values of (continuously measured) proportions
of one or more of the ZCTA proportions for the characteristics that LASSO has selected for our model
with observable heterogeneity. NOTE: “county” reference in figure caption will be corrected to “zcta” in
subsequent revision.
28Again, outlier proportions of one or more characteristics in ZCTA populations account for outlier WTP
estimates.
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our model a representative household in each of the 33,300 ZCTAs in the lower-48 states
of the U.S. For each ZCTA, we make a large number of draws from the joint distribution
of our parameter estimates and calculate an estimate of WTP for each draw. Then we
calculate both the mean and median WTP estimates for that ZCTA. Then we can map
the spatial variation in predicted median WTP estimates in each ZCTA. For our “basic
program” example, this spatial heterogeneity is shown in the map in Figure 5.
For our arbitrarily chosen “alternative program” example, different people’s
marginal WTP for the potential distributional consequences of non-basic cap-and-trade
programs can be illustrated. The spatial heterogeneity in median WTP for our alternative
program is shown in the map in Figure 6.
3.5 Directions for Future Research
Based on our study, respondents do not universally have strong preferences for
the percent of permits auctioned or the uses of the auction revenue, although our mixed
logit model with correlated marginal utilities suggest there is significant heterogeneity
across the population in preferences for the share of permits auctioned and the share
of revenue allocated to workers and communities. Thus, people’s auction and revenue
recycling preferences might vary across the population in ways that cancel out, on
average. Certainly, our LASSO-selected heterogeneity included in Model (5) suggests
that people are not universally indifferent to these attributes.
Future explorations of models allowing for attribute interactions are also a
possible extension of our work. Another possible explanation for the apparent lack of
importance of some cap-and-trade program design features (such as the percent of permits
auctioned, and the uses of auction revenue) could, of course, be that our survey was
overly complex for the average respondent. Statistically insignificant marginal utility
estimates may be a result of inattention to these features on the part of a sufficient number
of respondents. Further analysis of a relationship between respondents’ measured and
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self-reported attention to different program features may help clear up what is going on
with these less-robustly estimated average marginal utilities.
We are not yet entirely confident about the reliability of our benefit-function
transfer exercise, where we estimate our model of heterogeneous preferences based on
observable ZCTA-level characteristics for each of our 1050 Oregon respondents. We use
this model of ZCTA-level representative preferences to extend our predictions of WTP
for specific types of cap-and-trade programs to all ZCTAs in the lower-48 U.S. states. We
plan to enhance our model with ZCTA-level observable heterogeneity to include county-
level vote shares for the 2020 Presidential election. Given that our latent class model with
heterogeneity in terms of respondent ideology and climate-change attitudes achieved the
highest maximized log-likelihood of all our models, we expect that voting data (while
available nationally only at the county level, as opposed to the ZCTA level) may greatly
improve the predictive power of our model. As a strategy for limiting the influence of
outliers in our benefit-transfer exercise, we may also explore binning for our continuous
ZCTA proportions.
3.6 Conclusions
We have described a choice-experiment study of preferences over a variety of
attributes of potential carbon cap-and-trade programs to be implemented at the state
level. We have considered specifications that assume homogeneous preferences, as well
as heterogeneous preferences. In the second category, we include a random-preferences
model with purely unobservable heterogeneity, two different latent-class specifications
(one with class membership determined by a small set of respondent characteristics and
one with class membership determined by respondent attitudes/ideologies), and a model
with respondent neighborhood-level observable heterogeneity only (designed to facilitate
benefit-function transfer on a national scale).
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For our models with a single central tendency for marginal utilities (i.e.,
Model (1)-homogeneous clogit, and Model (2) (independent mixed logit), the preference
parameters are statistically significant for (a) cost per month, (b) an any-program
indicator, (d) carbon emission reductions, (d) carbon-intensive jobs, (e) green jobs, and
(f) additional regulations.29
Our estimate of average MWTP for a 1.0 proportional change in carbon emissions
by 2050 is between about $150 and $200, including the wider variety of models also
discussed in Stanford and Cameron (2022). However, proportional changes that large (i.e.
100 percent) were not included in our study. A recent proposal by the state of Oregon
suggests reducing emissions by 45% relative to 1990 levels by 2035 and by 80% relative
to 1990 levels by 2050. Graphics in our survey for the time trend in emissions for Oregon
suggests that 1990 levels were about 57 million metric tons of carbon dioxide equivalent,
and that 2021 levels at the time of the survey were about 61 million metric tons. Our
survey described the emissions reduction target as "the percent reduction of total annual
carbon emissions in Oregon by the year 2050, relative to Oregon’s current carbon
emissions. The suggested 2050 policy target then suggests reducing total emissions to
just 11.4 tons. This 80% emissions reduction was the largest proportional reduction in
our randomized choice experiment designs (where we asked respondents to consider
reductions between 10% and 80%. But a reduction from the current 61 million tons to
just 11.4 tons would be a about an 81% reduction, or a “Prop change in C emissions” of -
0.81. For our fixed coefficients logit specification, the MWTP estimate implies an average
willingness to pay, per month, of $153 * .81 = $124 to achieve the state’s goal of roughly
29One caveat relating to these results is that our sample-selection correction method, upon which these
results are based, is currently an ad hoc approach based on individual deviations from the mean survey
response propensity in among eligible respondents. There is some evidence that preferences may differ to
some extent between the respondent sample and the general population. Our sample-selection treatment is
more-rigorous than most, but could still be improved upon. See a dissertation chapter in Mitchell-Nelson
(2022) for a more-sophisticated approach.
83
an 80% reduction by 2050. By a similar calculation, however, our correlated mixed logit
model implies an average willingness to pay, per month, of about $166. A rough interval
estimate would be about $120 to about $212 .
Our preliminary findings support that, in addition to the obvious cost and benefits
of a carbon reduction policy (cost and emissions reductions), a cap-and-trade program’s
effect on jobs is of great importance to the public. A consistent significant and positive
sign on the "Any Program" marginal utility estimate indicates that, on average, the
public is supportive of a carbon cap-and-trade policy, regardless of its specific attributes.
These two results, taken together, suggest that successful implementation of a carbon
program in Oregon is likely to be highly dependent on designing a policy that navigates
the contentious “just transition” debate.
In our models with heterogeneous preferences, the presence of additional
regulations to limit emissions of other pollutants is generally a statistically significant
determinant of support for carbon cap-and-trade programs. This result suggests the likely
importance of additional protections for local residents who live around facilities that may
buy large numbers of carbon permits if a cap-and-trade program is implemented.
Our estimates for the Social Benefits of Carbon (SBC) emissions reductions
represent a useful complementary measure of the extent to which society may value
these emissions reductions. The customary benefits measure is, instead, an avoided-
cost measure: the Social Cost of Carbon. The Social Cost of Carbon (SCC), or marginal
avoided impact of greenhouse gas, has received a considerable amount of attention.
Nevertheless, there is no consensus on the true size of the SCC. Depending on the
researcher, agency, administration, or country, the estimate of SCC varies widely. Under
the Obama administration the SCC has estimated at $50 per tonne (in 2020 US dollars)
of CO2, with a range of $15-$75, while the Trump administration revalued the SCC
at $1-$7 per tonne (Wagner et al. (2021)). Subsequently, the Biden administration has
84
established an interim central value of $51/ton, and a range between $14 and $152/ton. It
is not surprising that the official SCC is highly dependent on the presiding administration,
considering the strong partisan differences in WTP for carbon emissions reductions
identified in this study and other research. However, estimates for the SCC are also vary
markedly within the field of economics. This uncertainty is due in large part to the fact
that the question of how to properly measure the SCC is still up for debate (Pindyck
(2019)). Nevertheless, improving our estimation of the SCC is imperative to designing
appropriate climate change policies (Aldy, Kotchen, Stavins, and Stock (2021)).
Our Social Benefit of Carbon (reduction), or SBC, measures the overall social
willingness to pay for a one-tonne reduction in carbon emissions via a cap-and-trade
program where increased costs will be borne by individual households. Our estimate for
our homogeneous clogit is only $47/ton , but for our more-general mixed logit models,
the estimate is $61 (or as high as $64 in the correlated mixed logit reported in Stanford
and Cameron (2022)), consistent with the Obama and Biden administration.30 However,
our latent class models estimates reveals that different political and ideological groups in
society have substantially different SBC estimates.
In comparison to the SCC values laid out by past and current administrations, our
SBC estimates tend to be reasonably similar. This suggests reasonable convergent validity
for our estimates. This convergent validity is important because the Social Cost of Carbon
(SCC) is a fundamentally different way to measure the benefits of carbon emissions
reductions, based on avoided damages, compared to our Social Benefits measure, which is
based on individual willingness-to-pay for carbon reductions.
The consistency between the SCC and SBC measures suggests that the SBC
may be well-suited as an alternative way to measure the effects of carbon emissions on
30The Trump administration’s valuation of less than $10/ton is largely ignored as a legitimate estimate of
the SCC.
85
social welfare. This stated-preference approach has the potential to improve benefit-
cost analyses of public programs to reduce carbon emissions, and affords an option to
consider in more detail the distributional consequences of these policies to reduce carbon
emissions.
86
Figure 3. Distribution of predicted WTP for basic cap-and-trade program
Across 33,300 lower-48-state ZCTAs, distribution of predicted WTP for basic cap-and-
trade program (40% carbon emissions reduction and no other special features). Example:
split by terciles of the proportion of the population commuting by public transit. Overall
national median WTP = $70 per month.
87
Figure 4. Distribution of predicted WTP for alternative cap-and-trade program
Across 33,300 lower-48-state ZCTAs, distribution of predicted WTP for alternative cap-
and-trade program (“(-4,-1,1,5,3,3,1,1)” means 40% carbon emissions reductions,
10% decline in county carbon jobs, 10% increase in county green jobs, 50% of
permits auctioned, 30% of auction revenue to equipment, 30% of auction revenue to
workers/communities, includes additional regulations on other pollutants, and an “any
program” indicator switched on). Example: split by terciles of the proportion of ZCTA
population commuting by public transit. Overall national median WTP = $114 per
month.
88
89
Figure 5. Map of predicted WTP for basic cap-and-trade program
By ZCTA: predicted WTP for basic cap-and-trade program (40% carbon emissions reduction and no other special features)
90
Figure 6. Map of predicted WTP for alternative basic cap-and-trade program
By ZCTA: predicted WTP for alternative cap-and-trade program (40% carbon emissions reduction, 10% decrease in county
carbon jobs, 10% increase in county green jobs, 50% of permits auctioned, 30% of auction revenue to equipment, 30% of
auction revenue to workers/communities, additional regulations on other pollutants)
Table 9. Descriptive statistics for cap-and-trade programs and for
alternative ways of capturing individual preference heterogeneity
mean (std. dev.)
1. Cap-and-trade program attributes
(All models, n=6300 programs)
Monthly cost 195.31 (101.87)
Prop change in C emissions -0.456 (0.226)
Prop change in carbon jobs -0.112 (0.064)
Prop change in green jobs 0.110 (0.062)
Share of permits auctioned 0.458 (0.230)
Share of rev. for equip. 0.304 (0.213)
Share of rev. to workers 0.305 (0.215)
1=New regs other pollut. 0.495 (0.500)
2. Preference heterogeneity: Individual demographics
(Model 3, n=1050 respondents)
1=College graduate 0.427 0.495
1=Income greater than 75K 0.441 0.497
1=Identifies as non-male 0.527 0.499
1=Own age:18-34 0.335 0.472
1=Own age:65+ 0.215 0.411
1=Has no children -0.000 0.482
1=Knows ancestors beyond gg grndprts 0.403 0.490
1=Has resided in Oregon 18+ years 0.191 0.393
1=Expect reside Oregon 20+ years 0.224 0.417
3. Preference heterogeneity: Ideology and opinions about climate change
(Model 4, n=1050 respondents)
1=Identifies as Democrat 0.420 (0.494)
1=Identifies as Republican 0.246 (0.431)
1=Ideology:Strongly liberal 0.178 (0.383)
1=Ideology:Somewhat liberal 0.207 (0.405)
1=Ideology:Somewhat conservative 0.164 (0.370)
1=Ideology:Strongly conservative 0.099 (0.299)
1=Str.agree clim.change threat 0.592 (0.491)
1=Agree clim.change a threat 0.223 (0.416)
1=Disagree clim.change a threat 0.048 (0.213)
1=Str.disagree clim.change a threat 0.024 (0.152)
1=Str.agree clim.change human-caused 0.450 (0.497)
1=Agree clim.change human-caused 0.309 (0.462)
1=Disagree clim.change human-caused 0.068 (0.251)
91
Table 10. Descriptive statistics for ZCTA-level heterogeneity in preferences selected by
LASSO for Model 5
Compare means (and standard deviations) for estimating sample, for all Oregon ZCTAs,
for National (lower-48 U.S. states) ZCTAs to be employed in benefits-function transfer
exercise
(1) (2) (3)
Est. sample Oregon National
ZCTA ZCTA ZCTA
data data data
(unwgtd)
mean/sd mean/sd mean/sd
ZCTA pr:Two or more races 0.077 0.064 0.046
(0.027) (0.050) (0.055)
ZCTA pr:American Indian/Alaska Native 0.010 0.017 0.014
(0.012) (0.061) (0.077)
ZCTA pr:Asian 0.048 0.018 0.022
(0.055) (0.033) (0.055)
ZCTA pr:Native Hawaiian/Pacific Islander 0.004 0.002 0.001
(0.005) (0.007) (0.006)
ZCTA pr:Other lang., but English good 0.100 0.060 0.071
(0.059) (0.065) (0.103)
ZCTA pr:Divorced or separated 0.143 0.144 0.129
(0.031) (0.070) (0.080)
ZCTA pr:High school grad. (incl. equiv.) 0.220 0.279 0.323
(0.084) (0.129) (0.149)
ZCTA pr:Bachelor’s degree 0.219 0.164 0.159
(0.094) (0.104) (0.110)
ZCTA pr:Income=10K or less 0.132 0.144 0.139
(0.034) (0.075) (0.083)
ZCTA pr:Income=15K to 25K 0.124 0.142 0.132
(0.030) (0.091) (0.075)
ZCTA pr:Income=65K to 75K 0.044 0.040 0.039
(0.012) (0.038) (0.035)
ZCTA pr:Native US cit.; born outside US 0.013 0.009 0.010
(0.006) (0.010) (0.020)
ZCTA pr:Indus=Mine/quarry/oil/gas extr. 0.001 0.003 0.010
(0.002) (0.027) (0.040)
ZCTA pr:Indus=Wholesale trade 0.025 0.022 0.023
(0.012) (0.031) (0.035)
ZCTA pr:Indus=Utilities 0.008 0.010 0.011
(0.006) (0.020) (0.028)
ZCTA pr:Indus=Information 0.016 0.014 0.013
(0.011) (0.027) (0.025)
ZCTA pr:Indus=Real estate/rent/lease 0.020 0.016 0.014
(0.011) (0.020) (0.028)
ZCTA pr:Indus=Mgt. of companies/enterp 0.002 0.001 0.001
(0.003) (0.003) (0.004)
Continued on next page
92
Table 10 – continued from previous page
(1) (2) (3)
Est. sample Oregon National
ZCTA ZCTA ZCTA
data data data
(unwgtd)
ZCTA pr:Indus=Arts/entert./recr. 0.021 0.021 0.018
(0.016) (0.042) (0.038)
ZCTA pr:Indus=Public administration 0.047 0.057 0.050
(0.029) (0.083) (0.063)
ZCTA pr:Smartphone 0.883 0.792 0.783
(0.049) (0.189) (0.187)
ZCTA pr:Tablet/portable wireless 0.650 0.577 0.557
(0.073) (0.179) (0.186)
ZCTA pr:Other computer only 0.000 0.000 0.000
(0.001) (0.001) (0.004)
ZCTA pr:Dial-up only 0.003 0.006 0.004
(0.004) (0.019) (0.019)
ZCTA pr:Broadband satellite internet 0.064 0.129 0.094
(0.048) (0.144) (0.099)
ZCTA pr:Heat=Bottled tank LP gas 0.016 0.051 0.148
(0.027) (0.096) (0.188)
ZCTA pr:Heat=Fuel oil kero etc. 0.013 0.043 0.075
(0.017) (0.081) (0.166)
ZCTA pr:Heat=Solar energy 0.001 0.001 0.001
(0.003) (0.006) (0.009)
ZCTA pr:Heat=Other fuel 0.007 0.013 0.013
(0.011) (0.021) (0.039)
ZCTA pr:Heat=No fuel used 0.004 0.005 0.006
(0.006) (0.012) (0.020)
ZCTA pr:Commute=10 min or less 0.158 0.214 0.156
(0.085) (0.183) (0.145)
ZCTA pr:Commute=25 to 29 min 0.066 0.053 0.065
(0.033) (0.055) (0.070)
ZCTA pr:Commute=45 to 59 min 0.065 0.080 0.083
(0.041) (0.106) (0.088)
ZCTA pr:Commute=60 min or more 0.058 0.081 0.091
(0.035) (0.102) (0.099)
ZCTA pr:Commute=1 vehicle avail 0.204 0.150 0.163
(0.087) (0.118) (0.132)
ZCTA pr:Commute=2 vehicles avail 0.399 0.346 0.373
(0.072) (0.165) (0.168)
ZCTA pr:Commute=public transp (not taxi) 0.036 0.013 0.015
(0.041) (0.031) (0.054)
ZCTA pr:Commute=other means 0.189 0.199 0.128
(0.091) (0.172) (0.126)
Observations 1050 430 33300
93
94
Table 11. Differences in baseline marginal utility parameter estimates across alternative specifications
For comparison, differences in baseline marginal utility parameter estimates across alternative specifications. Models 2 through 8 include
additional parameters that allow for heterogeneous preferences, to be presented in subsequent tables.
Model (1) (2) (3) (4) (5)
Homogeneous Independent Latent Class, demographics Latent Class, ideology For transfer
clogit mixed logit class 1 class 2 class 1 class 2 (when shifters=0)
Monthly cost -0.00308∗∗∗ -0.00843∗∗∗ -0.00465∗∗∗ -0.0127∗∗∗ -0.00500∗∗∗ -0.0164∗∗∗ -0.00344∗∗∗
(0.000290) (0.000846) (0.000447) (0.00132) (0.000395) (0.00218) (0.000305)
1=Any program 0.224∗ 0.406 1.319∗∗∗ -0.957∗∗∗ 1.268∗∗∗ -1.747∗∗∗ 0.239∗∗
(0.115) (0.275) (0.186) (0.346) (0.161) (0.565) (0.118)
Prop change in C emissions -0.469∗∗∗ -1.650∗∗∗ -0.954∗∗∗ -1.454∗∗∗ -0.909∗∗∗ -1.458∗∗ -0.541∗∗∗
(0.139) (0.270) (0.223) (0.416) (0.196) (0.639) (0.144)
Prop change in carbon jobs 1.433∗∗∗ 4.607∗∗∗ 2.908∗∗∗ 3.521∗∗ 2.638∗∗∗ 2.519 1.539∗∗∗
(0.448) (0.802) (0.656) (1.502) (0.590) (2.141) (0.463)
Prop change in green jobs 0.945∗∗ 4.114∗∗∗ 3.668∗∗∗ 0.585 2.949∗∗∗ 1.295 1.117∗∗
(0.457) (1.118) (0.864) (1.362) (0.710) (1.940) (0.480)
... × (dm:R̂P) -0.702 -3.579 2.796∗∗∗ -0.210 1.183 -2.428 -0.626
(0.481) (2.794) (1.067) (1.668) (0.801) (2.577) (0.555)
Share of permits auctioned 0.0346 -0.0330 -0.0262 0.146 0.00734 0.311 0.0321
(0.117) (0.195) (0.185) (0.352) (0.163) (0.508) (0.122)
Continued on next page
95
Table 11 – continued from previous page
Share of rev. for equip. -0.205 -0.300 -0.0362 -0.536 -0.108 -0.282 -0.162
(0.128) (0.225) (0.199) (0.398) (0.177) (0.648) (0.134)
Share of rev. to workers 0.170 0.537∗∗ 0.316 0.674∗ 0.292 1.004∗ 0.185
(0.127) (0.267) (0.204) (0.383) (0.179) (0.579) (0.131)
1=New regs other pollut. 0.186∗∗∗ 0.509∗∗∗ 0.289∗∗∗ 0.449∗∗∗ 0.264∗∗∗ 0.471∗ 0.184∗∗∗
(0.0528) (0.0994) (0.0831) (0.159) (0.0737) (0.253) (0.0547)
See subsequent tables for additional parameters in each specification
n/a Table 12 Table 13 Table 14 Table 15
Max. log-likelihood -4268.58 -3188.72 -3287.83 -3181.54 -3980.82
No. respondents 1050 1050 1050 1050 1050
No. choices 6300 6300 6300 6300 6300
No. alternatives 12600 12600 12600 12600 12600
Standard errors in parentheses. For all models, observations are weighted by county population proportions
in sample versus general population of the state.
Table 12. Additional parameters for Model (2) in Table 11
Marginal utility parameter standard deviation estimates for the
independent mixed logit specification
Coef. Est. Std. Err.
σ (1=Any program) -3.056∗∗∗ (0.269)
σ (Prop change in C emissions) -1.554 (3.810)
σ (Prop change in carbon jobs) -0.502 (2.723)
σ (Prop change in green jobs) -3.845 (2.432)
σ (Prop change in green jobs × dm:R̂P) 11.48∗∗∗ (2.052)
σ (Share of permits auctioned) -0.134 (0.429)
σ (Share of rev. for equip.) -1.006 (1.569)
σ (Share of rev. to workers) -2.103 (3.141)
σ (1=New regs other pollut.) -0.703∗∗ (0.293)
Table 13. Additional parameters for Model (3) in Table 11
Submodel for Class 1 membership propensity as a function of
demographic variables.
Class 1 membership Coef. Est. (Std. Err.)
1=College graduate 0.338∗∗ (0.152)
1=Income greater than 75K 0.213 (0.153)
1=Identifies as non-male -0.402∗∗∗ (0.142)
1=Own age:18-34 0.779∗∗∗ (0.172)
1=Own age:65+ -0.108 (0.184)
1=Has no children -0.00796 (0.154)
1=Knows ancestors beyond gg grndprts -0.385∗∗∗ (0.142)
1=Has resided in Oregon 18+ years -0.254 (0.161)
1=Expect reside Oregon 20+ years 0.311∗∗ (0.153)
Constant 0.194 (0.236)
96
Table 14. Additional parameters for Model (4) in Table 11
Submodel for Class 1 membership propensity as a function of
ideology and opinions about climate change.
Class 1 membership Coef. Est. (Std. Err.)
1=Identifies as Democrat 0.216 (0.213)
1=Identifies as Republican 0.432∗ (0.254)
1=Ideology:Strongly liberal 0.157 (0.275)
1=Ideology:Somewhat liberal 0.363 (0.252)
1=Ideology:Somewhat conservative -0.123 (0.258)
1=Ideology:Strongly conservative -0.386 (0.342)
1=Str. agree clim. change a threat 1.906∗∗∗ (0.336)
1=Agree clim. change a threat 1.200∗∗∗ (0.301)
1=Disagree clim. change a threat -0.587 (0.670)
1=Str. disagree clim. change a threat -2.131 (1.439)
1=Str.agree clim. change human-caused 0.793∗∗∗ (0.294)
1=Agree clim. change human-caused 0.602∗∗ (0.257)
1=Disagree clim. change human-caused -0.702 (0.504)
Constant -1.434∗∗∗ (0.287)
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Table 15. Additional parameters for Model 5 in Table 11
LASSO-selected systematic variation in marginal utilities according to ZCTA-
level characteristics (controlling for demeaned individual fitted response
propensity)
Heterogeneity Coef. Est. (Std. Err.)
1=Any program
... × (ZCTA pr:Two or more races) 7.470∗∗∗ (1.350)
... × (ZCTA pr:Asian) 0.0864 (1.888)
... × (ZCTA pr:Divorced or separated) 7.050∗∗∗ (1.423)
... × (ZCTA pr:High school grad. (incl. equiv.) -1.680 (1.108)
... × (ZCTA pr:Bachelor’s degree) 3.476∗∗∗ (1.131)
... × (ZCTA pr:Income=10K or less) -4.391∗∗∗ (1.158)
... × (ZCTA pr:Income=15K to 25K) 4.976∗∗∗ (1.750)
... × (ZCTA pr:Income=65K to 75K) -10.53∗∗∗ (3.156)
... × (ZCTA pr:Native US cit.; born outside US) 14.55∗∗ (6.239)
... × (ZCTA pr:Indus=Utilities) 4.123 (9.146)
... × (ZCTA pr:Indus=Public administration) -0.500 (1.933)
... × (ZCTA pr:Smartphone) 5.950∗∗∗ (1.125)
... × (ZCTA pr:Tablet/portable wireless) -1.785∗∗ (0.822)
... × (ZCTA pr:Broadband satellite internet ) 0.0220 (1.722)
... × (ZCTA pr:Heat=Bottled tank LP gas) 0.968 (3.289)
... × (ZCTA pr:Heat=Fuel oil kero etc.) -11.83∗∗∗ (2.187)
... × (ZCTA pr:Commute=25 to 29 min) 0.201 (1.085)
... × (ZCTA pr:Commute=45 to 59 min) 0.483 (1.528)
... × (ZCTA pr:Commute=1 vehicle avail) -1.207∗ (0.652)
... × (ZCTA pr:Commute=2 vehicles avail) -2.606∗∗∗ (0.618)
... × (ZCTA pr:Commute=public transp (not taxi) -0.194 (2.060)
... × (ZCTA pr:Commute=other means) 1.476∗∗ (0.742)
Prop change in C emissions
... × (ZCTA pr:Broadband satellite internet ) -3.047 (2.946)
... × (ZCTA pr:Commute=10 min or less) 3.188∗∗∗ (0.982)
... × (ZCTA pr:Commute=60 min or more) -6.705∗∗∗ (2.060)
Prop change in carbon jobs
... × (ZCTA pr:Asian) 10.71 (8.659)
... × (ZCTA pr:Indus=Wholesale trade) 52.94∗∗ (21.66)
... × (ZCTA pr:Indus=Mgt. of companies/enterp) -16.22 (103.7)
... × (ZCTA pr:Indus=Arts/entert./recr.) -19.87 (17.40)
... × (ZCTA pr:Heat=Bottled tank LP gas) -32.60 (30.42)
Prop change in green jobs
... × (ZCTA pr:Indus=Real estate/rent/lease) -114.6∗∗∗ (26.28)
... × (dm:R̂P) -0.626 (0.555)
Share of permits auctioned
... × (ZCTA pr:Asian) -5.520∗∗ (2.716)
... × (ZCTA pr:Native HI/Pacific Islander) 32.33∗∗∗ (11.80)
... × (ZCTA pr:Indus=Information) 1.212 (6.190)
... × (ZCTA pr:Indus=Mgt. of companies/enterp) 4.873 (32.54)
... × (ZCTA pr:Dial-up only) 38.82∗∗∗ (14.94)
... × (ZCTA pr:Heat=Other fuel) -18.93∗∗∗ (6.284)
Continued on next page
98
Table 15 – continued from previous page
... × (ZCTA pr:Heat=No fuel used) -28.23∗ (16.59)
... × (ZCTA pr:Commute=45 to 59 min) -3.744 (2.749)
... × (ZCTA pr:Commute=public transp (not taxi)) 7.937∗∗ (3.466)
Share of rev. for equip.
... × (ZCTA pr:Other lang., but English good) -5.201∗∗∗ (1.728)
... × (ZCTA pr:Indus=Mine/quarry/oil/gas extr.) 93.14 (59.57)
... × (ZCTA pr:Indus=Mgt. of companies/enterp) -33.82 (37.00)
... × (ZCTA pr:Indus=Public administration) -14.90∗∗∗ (5.314)
... × (ZCTA pr:Heat=Solar energy) 47.07 (33.12)
Share of rev. to workers (none)
... × (ZCTA pr:Asian) -2.663 (2.369)
... × (ZCTA pr:Indus=Mine/quarry/oil/gas extr.) 47.53 (69.20)
... × (ZCTA pr:Indus=Utilities) 37.19∗ (21.56)
... × (ZCTA pr:Heat=No fuel used) -67.21∗∗∗ (19.46)
1=New regs other pollut.
... × (ZCTA pr:American Indian/Alaska Native) -9.992∗∗ (4.767)
... × (ZCTA pr:Indus=Mine/quarry/oil/gas extr.) 35.62 (31.46)
... × (ZCTA pr:Other computer only) 117.6∗∗∗ (44.12)
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100
Table 16. For comparison, different implications of estimated utility parameters across specifications
Model (1) (2) (3) (4) (5)
Homogeneous Independent Latent Class, demographics Latent Class, ideology For transfer
clogit mixed logit class 1 class 2 class 1 class 2 (when shifters=0)
SBC reduct. (dollars/ton) 47 61 64 35 56 28 49a
MRS(cbn jobs, grn jobs) @ mix now 1.72 1.27 .90 6.81 1.01 2.20 1.56
(-.21, 3.64) (.51, 2.03) (.33, 1.46) (-24.9, 38.53) (.37, 1.66) (-5.42, 9.83) (-.03, 3.15)
MWTP(1=Any program) 73 48 284 -75 253 -107 70
(1.53, 144) (-12, 108) (199, 369) (-134, -17) (187, 320) (-183, -31) (4.17, 135)
MWTP(Prop change in C emissions) -153 -196 -205 -115 -182 -89 -157
(-238, -67) (-264, -127) (-294, -117) (-178, -51) (-254, -110) (-165, -13) (-236, -78)
MWTP(Prop change in carbon jobs) 466 547 626 277 527 154 447
(169, 763) (341, 753) (327, 925) (45, 510) (285, 770) (-104, 412) (174, 720)
MWTP(Prop change in green jobs) 307 488 789 46 589 79 325
(12, 603) (253, 724) (389, 1190) (-165, 257) (295, 884) (-155, 313) (47, 603)
MWTP(Share of permits auctioned) 11 -3.91 -5.64 12 1.47 19 9.32
(-63, 86) (-49, 42) (-84, 72) (-42, 65) (-62, 65) (-41, 79) (-60, 78)
MWTP(Share of rev. for equip.) -67 -36 -7.8 -42 -22 -17 -47
(-149, 16) (-88, 17) (-92, 76) (-104, 20) (-91, 48) (-95, 61) (-124, 30)
MWTP(Share of rev. to workers) 55 64 68 53 58 61 54
(-26, 137) (2.97, 124) (-19, 155) (-6.62, 113) (-12, 129) (-8.38, 131) (-22, 129)
MWTP(1=New regs other pollut.) 60 60 62 35 53 29 54
(25, 96) (36, 85) (25, 99) (9.9, 61) (23, 83) (-2.38, 60) (21, 86)
Notes: Auction-related attributes did not tend to bear statistically significant coefficients, so we do not report their MWTP.
aDepends on factors affecting MU(C emissions). bInterval estimates for this latent class model pending re-calculation. cA simple sign change
converts MWTP for the status quo option, regardless of the attributes ofthe proposed program, into the corresponding MWTP for "Any program".
dHeterogeneous across counties with different characteristics, so we do not report any single value.
CHAPTER IV
OREGUNIANS AND THE GUN-CONTROL PARADOX
We study the impacts of newly passed gun legislation on the demand for firearms.
We focus on Oregon, where voters passed Measure 114 in a referendum in November
of 2022. After weeks of public debate and news coverage, the measure narrowly passed
with 50.7 percent of the votes. We study the effects of this result on the demand for guns
proxied by background checks. We find background checks surged by 400 percent for
six weeks following the vote. After a judge’s decision prevented the law from taking
immediate effect, background checks fell from their all-time high, but persisted at roughly
100 percent above their original levels, even five months after the original passage of
the measure. Additionally, we conduct the first analysis of background check data at the
county-daily level, using Oregon State Police administrative data. We find significant
heterogeneity in Oregonians’ firearm purchasing behavior across counties. The surge
in firearm demand resulting from Oregon’s Measure 114 exemplifies the gun-control
paradox and provides a cautionary tale to policymakers.
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4.1 Introduction
The United States leads the developed world in gun deaths and has seen a steady
increase in annual deaths in the last two decades. Indeed, 2021 marked an unfortunate
high point, with nationwide gun deaths totaling 48,830 (Gramlich, 2023). Mass shootings
and other high-profile gun accidents continue to make headlines, while federal changes to
gun laws remain essentially non-existent since the expiration of the Assault Weapons Ban
in 2004.
While federal policies stagnate, some states have begun to limit access to firearms.
Even Texas is debating an increase in the minimum legal age to purchase high-capacity
rifles to twenty-one in response to the highly publicized tragedy at Uvalde in May of
2022. Oregon also recently joined a growing set of states moving to pass gun control
measures intended to improve firearm safety. Oregon’s recent legislation came about
through a public referendum process, appearing on the November 2022 ballot as Measure
114. If passed, this referendum promised background checks for all gun sales, restrictions
on magazines, and a new permit-to-purchase program. The last provision attracted
considerable debate in the final weeks leading up to the election.
On the surface, one may expect the provisions specified in Measure 114 would be
effective in reducing long-run gun deaths and accidents. Indeed, both D. Webster, Crifasi,
and Vernick (2014) and Williams Jr (2020) find evidence that the repeal of Missouri’s
permit-to-purchase program led to more gun purchases and additional homicides.
Likewise, the passage of a permit-to-purchase restriction in Connecticut was followed
by decreases in homicides (Rudolph, Stuart, Vernick, & Webster, 2015). Crifasi, Meyers,
Vernick, and Webster (2015) study both Missouri’s and Connecticut’s permit-to-purchase
programs and finds evidence that these restrictions serve to reduce suicide risk as well
(Rudolph et al., 2015). However, if individuals anticipate the laws, the laws’ potential
benefits may be attenuated (or even entirely offset).
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Anticipatory behavior has been found in many other contexts. Becker, Grossman,
and Murphy (1994) find that while smokers cut their smoking behavior anticipating future
tax hikes, they also stockpile cigarettes to avoid future taxes. In labor economics, similar
anticipation effects are seen in program participation, referred to as an “Ashenefelter
Dip,” and in environmental economics, this has been noted for climate change policy,
referred to as a “Green Paradox” (Ashenfelter & Card, 1985; Sinn, 2015). We find
evidence that the salient threat of the implementation of Measure 114 led to a roughly
400 percent increase in gun sales.
We contribute to a growing body of literature that suggests there is a “steel
paradox.” While gun control policy may have benefits in the long-term, it may be met
with short-term increases in firearm demand. Depetris-Chauvin (2015) finds President
Obama’s election saw increases in background checks despite the Obama administration
never leading any federal gun control policies. Levine and McKnight (2017) find that the
Sandy Hook mass shooting led to increases in firearm purchases and gun accidents, again
amidst no movement in federal legislation (and very little change in state-level laws). So
while policies like a permit-to-purchase program and increased background checks may
reduce gun sales in the long run, the short-run effects also warrant consideration for gun
policy in the United States.
The effects of gun availability on local crime patterns have long been debated
(Kleck, 2004). Theoretically, gun ownership could create a deterrent effect against
many types of crime. However, the bulk of the literature suggests that more guns lead
to more crime, rather than less. Duggan (2001) finds several proxies for gun ownership
are associated with increases in homicide risk and increases in the risks for other violent
crimes as well. Cook and Ludwig (2006) find that gun ownership, proxied by the fraction
of suicides involving guns, corresponds to higher rates of violent crime. Likewise,
Billings (n.d.) finds that regions which exhibit more firearm background checks after
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national high-profile mass shootings see increases in their local violent crime rates, and
increases in property theft (particularly those which involve firearms). Thus, rather than
deterring crimes, guns themselves are often the targets of crime.
We add to this growing literatur with evidence that suggests that there is a “steel
paradox” for firearms policy. In the long run, the passage of a substantive restriction like
a permit-to-purchase program may increase public safety by reducing the number of guns
in circulation—or preventing “dangerous” purchases. However, the passage of a permit-
to-purchase program will likely spawn anticipation effects. To estimate short-run and
medium-run effects, we use the National Instant Background Check System (NICS) data
from the FBI. Using national data at the month-state level and a synthetic difference-in-
differences approach (Arkhangelsky, Athey, Hirshberg, Imbens, & Wager, 2021), we find
evidence of strong anticipation effects immediately after the passage of Oregon’s Measure
114. We also use NICS data at the county-day level from Oregon’s state police, focusing
on the temporal patterns of anticipation effects and their geographic heterogeneity. We
find that background checks actually began to increase in the weeks before the election
and then immediately jumped after the outcome of the vote was known. We also find
that background checks subsided after a judge halted the implementation of the new
law. Still these checks remain elevated relative to their earilier baseline level, before
the measure was first proposed. We also examine the heterogenous impact of Measure
114 across Oregon counties. Roughly equal shares of the increase in firearm sales can
be attributed to counties that voted for or against the measure. However, the per capita
effect is roughly fifty-percent larger for counties that largely did not support the measure.
In counties most strongly opposed to Measure 114, we observe weeks in which the
number of background checks translates to nearly 1% of the local population purchasing
a firearm. It’s noteworthy that in absolute magnitudes, the anticipation effects we estimate
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for Oregon are much larger than the Obama effect, the Sandy Hook effect, or the surge in
gun purchases observed early during the COVID19 pandemic.
4.2 Background
4.2.1 Gun laws in the United States. Conversations surrounding firearms
and firearm regulation play an increasingly important role in American politics. The
firearm-regulation debate, and research concerning firearms, have both evolved over
time in focus and framing (Carlson, 2020; Steidley & Yamane, 2022). However, the
central tenets of proponents and opponents of firearm regulation remain relatively
unchanged. Those in favor of regulation often cite the large number of injuries and deaths
related to firearms each year (the CDC reported over 48,000 firearm-related deaths in
2021, and that firearms were the leading cause of death for children as of 2020). On
the other hand, opponents of regulation frequently argue that access to firearms is a
constitutional right and that firearms are an important tool for citizens to keep themselves
safe. Carlson (2020) highlights that both sides argue that “evidence matters” and the other
side “ignore[s] the facts.”
Currently, firearms are regulated at both the national and state levels. Since
the National Firearms Act of 1934, expansion of federal regulation has been modest.1
Until the passage of the Bipartisan Safer Communities Act (2022) under the Biden
administration, the most recent national-level firearm regulation policies were the Brady
Handgun Prevention Act (1993) and the Federal Assault Weapon Ban (1994–2004). In the
latter half of the 20th century and the early 21st century, federal-level firearm regulation
has often been catalyzed by either high-profile firearm-related incidents or by rising crime
rates.
In contrast to the few changes in federal regulation, there have been significant
changes to state-level firearm laws in the United States over the last 20 years. Some states
1Vizzard (2015) provides a good overview of firearm policy in the United States.
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have enacted more-stringent regulations on firearm ownership, while others have loosened
their laws. A thorough discussion of firearm laws is beyond the scope of this paper.
However, we briefly discuss three firearm-related laws relevant to this paper: background
check, permit-to-purchase, and high-capacity magazine laws.
Background Checks: Federal law requires a background check be performed
through the FBI’s National Instant Criminal Background System (NICS) for all purchases
from a federal firearms licensee (FFL), manufacturer, or importer. There are several
modifications states have made to this federal mandate. First, depending on state law,
FFLs either communicate with the NICS directly or alert a state-designated point of
contact that then communicates with the NICS. Second, states have adopted laws that
expanded background check requirements beyond FFL sales. For example, states with
Universal Background Check laws (UBC) require background checks for all firearm
sales and transfers (e.g., sales between private parties, sales at gun shows, or gifts).
Third, states may run their own background checks that access state records that are not
included in a NICS background check. Finally, state laws may allow for the substitution
of an ATF-qualified alternate permit that can act in place of an NICS background check.
However, an individual must undergo a background check to obtain the permit.
Permit-to-Purchase: A permit-to-purchase (P2P) law requires individuals a permit
or license before purchasing a firearm. In contrast to background checks, P2P laws have
been implemented only at the state level. To obtain a permit, an individual must apply
for a permit at a local agency. Typically, the local agency is a law enforcement agency,
and the application must be completed in person. Depending on state law, successfully
obtaining a permit may requirements in addition to a background check (e.g., a gun-
safety course). Like UBC laws, P2P laws ensure that all gunowners are subject to a
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background check. Some states have adopted both UBC laws and P2P laws, meaning
that a background check is performed for individual at the time of the permit application
and an additional time at the point of sale.
High-capacity magazine restrictions: The Federal Assault Weapon Ban of 1994
banned the manufacture, sale, and possession of new high-capacity magazines (more
than 10 rounds) for civilian use. However, it allowed individuals who already possessed
high-capacity magazines before the ban to keep them. The ban had a sunset provision and
expired in 2004. In response, several states have imposed limits on magazine capacity.
Due to the frequent use of high-capacity magazines in mass shooting events (MSE), high-
capacity magazines have come under renewed scrutiny.
Table 17 reports the status of background check, permit-to-purchase, and
high-capacity magazine laws in the United States. Twenty-one states have expanded
background check laws beyond the federal mandate. Fourteen of these states require
a background check at the point of sale for all firearm classes. Nine states require a
permit (or license) to purchase all or some classes of firearms. Missouri (2007), Nebraska
(2023), and North Carolina (2023) repealed their existing permit-to-purchase laws. 14
states have banned or restricted possession of high-capacity magazines.
4.2.2 Gun laws in Oregon. In November 2022, nearly two million Oregon
voters narrowly passed Measure 114, an initiative aimed to curb access to firearms and
high-capacity magazines. Measure 114 would require that buyers receive a permit from
local law enforcement prior to purchasing a firearm. In contrast to previous background
check requirements, Measure 114 would result in permits being denied more easily on
the basis of concerns over an individual’s psychological state. Additionally, permits are
contingent on demonstrated completion of a firearm safety course. Permits under Measure
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114 are valid for five years. Beyond the gun-permitting requirements, Measure 114 would
make it a criminal offense to possess magazines capable of holding ten or more rounds.
The passage of Measure 114 was controversial throughout Oregon and followed
a decade of gradually strengthening gun legislation in the state. Between 2015 and 2021,
Oregon expanded its background check data infrastructure, implemented a “red flag” law
enabling judges to order the removal of firearms from at-risk individuals upon a petition
from a household member or law enforcement agency, extended gun restrictions for those
under a restraining order or convicted of stalking, and mandated safe firearm storage
practices. With the added provisions of Measure 114, Oregon rose in Everytown’s gun
law strength rankings from 11th in the country to 9th in January 2023.
Although Oregon referenda typically become effective 30 days after passage,
uncertainty over how and when Measure 114’s implementation spread rapidly after the
election. Some sheriffs announced that they would not enforce provisions of the law, and
gun advocates challenged the constitutionality of Measure 114 in court. As of May 2023,
litigation was ongoing and Measure 114 had not been implemented.
In response to this uncertainty, in January 2023 Oregon lawmakers introduced
Senate Bill 348, which would implement the primary provisions of Measure 114.
Additionally, Senate Bill 348 would raise the minimum age for firearm purchasers. In
April 2023, the bill successfully passed out of committee but awaits a vote by the Senate.
4.3 Data
Measuring gun ownership Despite the prevalence of firearms in policy debates
and in the national dialogue, firearm-related data are scarce or inaccessible. Rather
than being a shortsighted blunder, this lack of data is often by design. For instance,
despite including thousands of detailed product categories, the Nielsen Consumer Panel
censors information about firearm purchases. One approach to filling this data gap has
been to conduct national firearm-ownership surveys (e.g., the NRA’s National Gun
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Owners Survey). However, this approach has several disadvantages. First, large-scale
surveys are conducted infrequently, and granular temporal analysis using this type of
data is not feasible. Second, surveys are always subject to sample selection bias, and
the representativeness of any voluntary survey is often a concern. Finally, regarding
selection bias, Urbatsch (2019) finds an increasing level of nonresponse over time for
firearm-ownership surveys—especially among Republicans and those who do not trust the
government.
In the absence of direct measures, researchers have employed a wide range of
firearm proxies varying from NRA membership to outdoor magazine subscriptions.
Firearm Suicides divided by total Suicides (FSS) and NICS FBI background checks seem
to have emerged as the two most popular proxies for firearm ownership.
Each proxy presents unique advantages and disadvantages for researchers (Cook
& Ludwig, 2019). For instance, FSS ensures that a gun is observed in the community,
thus avoiding challenges presented by issues like illegal firearm markets or inherited
firearms.2 However, due to the relative rarity of these events, using FSS as a proxy
for firearm ownership is challenging in areas with small populations or across time
(Cerqueira, Coelho, Fernandes, & Junior, 2018; Kleck, 2004).
Lang (2013), who was one of the first researchers to implement the FBI
background checks proxy, points out several drawbacks to using these background
checks as a proxy. In some states, if a buyer possesses an up-to-date CCW permit, they
may be excused from a background check when purchasing a firearm. On the other
hand, some states periodically run “permit-check” background checks on all permit
holders, regardless of a permit holder’s decision to buy a new firearm—compromising
the reliability of background checks as a proxy for gun purchases. Additionally, while
2Because medical records indicate whether a firearm was used in the suicide there is no ambiguity about
the presence of a firearm.
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the Brady Act requires background checks for all purchases from Federal Firearm
licensees (FFL), the federal government does not require background checks for private
sales or for sales at gun shows. While some states have enacted laws that expand
background checks for private and gun-show sales, many states have not. Finally, there
is evidence that compliance with federal law is not universal and that compliance levels
may vary systematically by geography (e.g., Castillo-Carniglia et al., 2018; Castillo-
Carniglia, Webster, & Wintemute, 2019; Hepburn, Azrael, & Miller, 2022). Despite these
drawbacks, Kim and Wilbur (2022) demonstrate that background checks outperform other
commonly used proxies.
OSP data This paper uses FBI background checks to proxy for firearm purchases.
Since the passage of the Brady Gun Act in 1993, the federal government has required that
all gun purchases from FFLs be conditioned on the results of a background check on the
buyer through the FBI’s National Instant Criminal Background Check System (NICS).
Our strategy to use FBI background checks as a proxy for firearm purchases is
common in firearm research. However, our background-check data are uniquely spatially
and temporally detailed. To date, research that uses background-check data relies on the
NICS FBI background check data aggregated to the month and state level. All FFLs
are required to run a background check through the NICS, but the particular entity that
contacts the NICS depends on state law. In some states, local law enforcement agencies
are appointed as intermediaries between sellers and the NICS. For other states, state laws
require FFLs and other covered sellers to contact the NICS directly. In Oregon, firearm
sellers contact the Oregon State Police (OSP), who then contact the NICS. Consequently,
the OSP maintains detailed records of all NICS background checks requested in Oregon.
The Oregon State Police (OSP) provided us with daily county-level background check
data—significantly improving the level of detail possible in our analysis. The data begin
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in February of 2018 and are appended every month. Currently, the overall period of
observation for the OSP data runs through March of 2023. The data also indicate the
status of each background check (i.e., Approved, Canceled, Denied, and Pending).
FBI NICS data We complement the OSP data with the publicly available FBI
NICS data. The FBI aggregates background data to the state-month level. As mentioned
before, federal law requires gun sales from FFLs to be conditioned on background checks
through the FBI’s NICS. Numerous states (e.g., California) have implemented laws that
expand background checks to other types of purchases (e.g., gun shows). These laws
are frequently referred to as Universal Background Checks (UBCs). However, because
background-check laws vary across states, comparing total background checks across
states is not always accurate. Fortunately, the FBI also distinguishes between the different
types of background check. For instance, the FBI data indicate whether the background
check was on behalf of an FFL (as opposed to a private sale) and also note the type of
firearm for which the background check was being run (e.g., handgun or long gun).
The observation period for our FBI data runs from January 2000 through April
2023. The data include Oregon’s background check data. The OSP data offer greater
granularity than the publicly available FBI data, but the OSP records do not indicate the
type of background check. A comparison the time-series of OSP data versus the time-
series of FBI data for Oregon in Figure 7 suggests that the OSP data likely do not include
permit checks. In the FBI data, Oregon agencies also requested very few background
checks for private gun sales. Consequently, we use the set of Non-private gun sales
among the FBI background checks for our analysis.
Additional data We use several additional data sources for our analysis. First, we
use the population data from the Census for state populations (2000-2022) and Oregon
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county populations (2018-2022).3 We use the data to calculate changes in per-capita
background checks. Given that there is considerable variation in the sizes of state and
county populations that may be correlated with the propensity to own firearms, measuring
background checks as a rate per capita is an essential adjustment to this measure.
We also use data from the New York Times for Oregon’s 2022 election results.
We look at both the referendum election results for Measure 114 and votes in the
contemporaneous Oregon governor race.
4.4 Methodology
The primary objective of our analysis is to examine how the firearm-purchasing
decisions of Oregonians respond to the proposal and passage of Measure 114. Due to
the granularity of the OSP data, we can track background checks at the daily level for
individual counties in Oregon. However, we do not have daily county-level data for
counties in other states. Thus we cannot simply compare the treated (Oregon counties)
to the control (non-Oregon counties). Our estimation strategy therefore uses two steps
to address this issue. Our first step is a proof of concept that Measure 114 has a causal
effect on background checks in Oregon. For this step, we use a synthetic difference-in-
difference (DiD) approach to compare month-state-level background checks in Oregon to
a synthetic Oregon comprised of a weighted mix of other states. We explain background
checks in State i at time t the following equation:
bgcit = β11(Oregoni)+β21(Postt)+β3(1(Oregoni)×1(Postt))+ εit
After establishing a causal effect of Measure 114 on background checks in
Oregon, we use the OSP data to examine responses over time to Measure 114 in more
temporal and geographic detail. More specifically, we measure changes in background
3The different time periods reflect county-level background data from the OSP beginning in February of
2018.
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checks at the daily and weekly levels and examine heterogeneity in these changes
across Oregon’s thirty-six counties. Our first approach is to examine the time-series
of background checks in Oregon. Given that we have already established a causal
relationship, a time-series model is perhaps the most informative method to employ as
we examine the behavior of Oregonians. We also use a time-series model to examine the
effect of a county’s support for Measure 114 on its response behavior.
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To complement our time-series model, we implement an event study to measure
the average treatment effect across counties in Oregon. We estimate this event study using
the following specification:
bgcit = β0 +βt1(Treated)+ εit (4.1)
We use the event study to pin down the date of when anticipatory firearm sales
begin in Oregon at a finer temporal level than is permited by the FBI background-check
data.
Next, we return to our initial synthetic-control DiD strategy to further examine
county-level heterogeneity. However, instead of comparing all of Oregon to a synthetic
Oregon, we now compare individual counties to synthetic counties. As mentioned,
county-level data are unavailable for other states. Instead, our synthetic counties are
compromised of a weighted mix of other entire states, excluding Oregon.
Finally, we explore heterogeniety in background checks across counties in
Oregon. We do so by splitting our OSP data by county-level election results for Measure
114. First, we split the data into two groups: counties where the majority of voters
(50%>) supported Measure 114 and counties where the majority of voters did not support
Measure 114. We use a time-series model to visualize the difference in behaviors.
Second, we split the data into quartiles—dictated by voting results for Measure 114 for
each county. Each quartile has nine Oregon counties. Again, use a time-series model to
visualize the difference in behaviors.
4.5 Results
4.5.1 Treatment period. Before we estimate the effects of Measure 114 on
background checks, we explore the timing of when Oregonians first began to respond
to the bill. An obvious choice is when Measure 114 passed on November 8th, 2022.
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However, Oregonians were likely aware of the bill ahead of election day and may have
responded in anticipation of its passage. To get a sense of Oregonians’ awareness of
Measure 114 prior to election day, we use Google Trends. We use the search “Measure
114” from January 2022 through April 2023. Figure 8 displays the results from Google
Trends. While we see a spike in searches during the week of the election, we also notice
that Google searches for “Measure 114” increase several weeks ahead of election day.
4.5.2 State-level synthetic control difference-in-difference. We use a
synthetic control difference-in-difference strategy to establish a causal relationship
between Measure 114 and background checks. First, we create a synthetic control
for Oregon as a whole, based on other states. We then use a difference-in-difference
specification to compare background checks in Oregon to a simulated counterfactual for
Oregon had Measure 114 not passed. Figure 9 illustrates the effect of Measure 114 with
background checks per capita as the outcome variable.4 The top panel compares Oregon
and synthetic Oregon over time, and the bottom panel plots the difference between the
two (Oregon minus synthetic Oregon). Figure 9 assumes that treatment begins only as of
November 2023. However, the results from Figure 8 suggest that treatment—namely,
anticipation of Measure 114 and its impact on Oregonians—may begin earlier than
November. Given that the data are aggregated at the monthly level for this part of the
analysis, we must choose between October and November 2022.
Figure 9 illustrate an enormous surge in background checks in anticipation of
Measure 114. The top panels of the figure confirm the findings in previous studies
that firearm purchases respond to mass shooting events (MSE) and other events—like
President Obama’s 2008 election and the onset of the COVID-19 pandemic. However, it
is striking how much larger was the response of Oregonians to Measure 114 compared
4Results for the effect of Measure 114 with the raw count of background checks as the outcome variable
can be seen in Appendix C.1.
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to any other event over the last 20 years. It is also worth noting that the bottom panels of
the figures suggest that Oregonians were more responsive than other similar states to the
effects of COVID-19.
We report additional results in Table 18, where we distinguish background checks
by type. We can observe that the lion’s share of the increase in background checks
concerned handgun sales. Table 19 reports the cumulative increase in background checks
in the five months since the passage of Measure 114. During our observation period
(November 2022 through March 2023), Measure 114 induced a cummulative increase
of about 150,000 background checks in Oregon. In per-capita terms, this translates to
approximately 3.5 background checks for every one hundred Oregonians.
4.5.3 Time-series models. As mentioned, in contrast with the FBI data, the
background check data provided by the Oregon State Police has much higher resolution,
being reported at the day and county level. This enables us to observe decisions about
purchasing firearms in greater detail. However, we are constrained in that the data do not
allow for an obvious counterfactual. Relying on the causal relationship established via our
state-level synthetic control results, we first examine the OSP data as a timeseries from
February 2018 through February 2023 aggregated, to the weekly level across all Oregon
counties—shown in Figure 10. Our decision to aggregate to the weekly level is motivated
by weekly patterns in the data. More specifically, there are sharp declines in background
checks on Sunday and Monday of each week. Figure 10 demonstrates a large but brief
spike in background checks during the week of 3/15/20, when the COVID-19 Pandemic
unofficially “began.” The other distinct spike in background checks occurs in conjunction
with the passage of Measure 114. In comparison to the spike related to COVID-19, this
surge in background checks is substantially larger in magnitude and lasts considerably
longer.
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To get a better understanding of responses to Measure 114, we use same the
weekly aggregated timeseries, but focus on the period between Januray 2022 and the
end of the OSP data in February 2023—as seen in Figure 11. Figure 11 shows that there
is anticipatory behavior beginning early in October 2022 (indicated in red), followed by a
prolonged surge in background checks that continues through the end 2022 (indicated in
blue).
Finally, Figure 12 shows daily background checks around the time of the passage
of Measure 114 on November 8th, 2022. To minimize day-of-week variation, we exclude
Monday and Sunday from the data.5 However, a weekly spike on Saturday is still evident
followed by fewer background checks on Tuesday. We can see an increase in background
checks beginning in early October (highlighted in red) that then surge with the passage
of Measure 114. “Black Friday,” the shopping event the day after the U.S. Thanksgiving
holiday, 17 days after the vote on Measure 114, is the high-water mark for background
checks. We omit Thanksgiving Day from the data to improve clarity of the trend of
background-check trend.6 For, roughly 2,000 background checks on 12/13/2022 and
12/14/2022 in the OSP data, it is not possible to attribute the background check to a
specific county. These checks were dropped, accounting for a sudden drop in background
checks (highlighted in yellow). We also see that background checks dipped around
Christmas Day (highlighted in green).
4.5.4 Event Study. We also use the OSP daily data by county to perform
a selection of event studies. Each county is a group in our event studies, but because
Measure 114 is a statewide law, each group has the same event date. We aggregate the
data for each county to the weekly level and begin our observation period in January
5Sharp dips in background checks occur on Monday and Sunday each week, and excluding them from
the figure paints a clearer picture than with their inclusion.
6The sharp decline in background checks on Thanksgiving Day reflect the closure of stores rather than a
change in the firearm purchasing behavior for Oregonians
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2022. We are not especially interested in the average treatment effect—the average
increase in background checks per county. However, these treatment studies allow us
to identify anticipatory behavior more accurately. We use two event dates for our event
studies: the week Measure 114 passed (the week starting 11/07/2022) and the week when
we see anticipatory behavior in our timeseries (starting 10/10/2022).
By comparing Figures 13 and 14 it is apparent that there is indeed anticipatory
behavior. When we designate the event date as the election week, we see that the weeks
preceding Measure 114 are consistently statistically negative—instead of the white noise
we would expect to see. In addition, we see that predictions are consistently statistically
negative starting seven weeks after our reference point, which again contradicts the
timeseries figures 10, 11, and 12. In contrast, when we designate our event date as the
week of 10/10/2022, we no longer see the consistently statistically significant negative
observations preceding Measure 114. We also observe that background checks do not
return to pre-Measure 114 levels in the immediately following weeks. Instead, they
remain positive and statistically significant.
4.5.5 County Heterogeneity. The temporal resolution of the OSP data
allows us to analyze heterogeneity in background checks across counties. We combine the
FBI and OSP data to perform a synthetic DiD for each county in Oregon. To create our
synthetic control for each Oregon county, however, we use non-Oregon state-level (rather
than county-level) background checks. Given that the FBI data are available only at the
monthly level, our analysis of county treatment effects must be constrained to the monthly
level. Table 20 reports the estimated treatment effect for each county, where the outcome
variable is background checks per 100,000 county residents. Each row in Table 20 reflects
the results of a distinct synthetic control model, where the counterfactual predicitions for
each Oregon county stem from a different set of weights on a different subset of Non-
Oregon states. There is significant variation across counties in the magnitudes of these
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estimates—most estimates are statistically significant and positive, apart from those
for Malheur and Wheeler Counties. Counties containing the largest urban centers (e.g.,
Multnomah County, which contains much of the metropolitan area associated with the
city of Portland) see relatively modest increases in background checks. In contrast, the
state’s more-rural counties (e.g., Harney County and Douglas County) featured much
larger per-capita increases in background checks.
We dig further into heterogeneity in county-level background checks by
differentiating county background checks by county voting results for Measure 114. We
do this in two ways. First, we separate counties into just two groups: counties that voted
>50% in support of Measure 114 and those that voted >50% in opposition to Measure
114. Figure 15 shows the timeseries of background checks for these two groups from
February 2018 through February 2023. The dependent variable in the top panel is total
background checks, and the dependent variable in the bottom panel is background checks
per 100,000 county residents. Figure 15 shows that while the total background checks
between the two groups of counties are comparable, the per-resident background checks
were roughly 300% larger for counties that voted in opposition to Measure 114. Figure
16 uses the same specifications as Figure 15 but focuses our attention on just the months
of 2022. Focusing on the weeks surrounding Measure 114, the bottom panel of Figure
16 indicates that the rates of per-capita background checks were over 50% higher for the
counties that voted against the law.
Next, instead of grouping counties simply by majority support for or
against Measure 114, we bin counties into quartiles of the voting percentage
distribution—determined by an equal number of counties for each quartile. Despite its
passage overall, most counties did not individually vote in favor of Measure 114. Across
counties, the range for he first quartile for support for Measure 114 is [11%, 20.8%]. For
the second quartile, it is (20.8%, 31%); for the third quartile, it is (31%, 43.5%]; and for
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the fourth quartile, it is (43.5%, 74%]. Figure 17 tells an even more striking story about
which Oregon counties supported Measure 114 and how they responded to its passage.
The top and bottom panels of Figure 17 again summarize the total background checks
and background checks per county resident, respectively. The small rural counties, with
the strongest opposition to Measure 114, are responsible for a small share of total checks,
but they saw massive increases in per-capita background checks. Comparing per-capita
rates of background checks between quartiles, we see that increases for counties in the
first and second quatrile were approximately twice as large as for counties in the fourth
quartile. Weekly per-capita rates for counties in the first and second quartile indicate that
there were multiple weeks where the number of firearm background checks was close to
1% of the population.
4.6 Discussion
We document large increases in Oregon’s gun-purchasing background checks
in response to the state’s restrictive firearm control law, Measure 114. We estimate a
cumulative increase of approximately 150,000 firearm sales resulting from Measure
114—equivalent to 3% of the state’s population purchasing firearms. We find that
the increase in background checks begins weeks ahead of Election Day—suggesting
anticipatory behavior even before the outcome of the vote is known. The increase in
background checks surges after the passage of Measure 114 and persists above baseline
levels for months afterward. The extant literature document other cases where citizens
have responded in anticipation of restrictive firearm laws (e.g., Balakrishna & Wilbur,
2022; Depetris-Chauvin, 2015; Iwama & McDevitt, 2021). The surge in firearm sales
following the passage of Oregon’s Measure 114 dwarfs estimates from similar studies
in duration and magnitude. Balakrishna and Wilbur (2022) documented increased
firearm sales when a Massachusetts law was reinterpreted, leading to a ban on certain
types of firearms. Iwama and McDevitt (2021) find that Massachusetts’ Gun Violence
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Reduction Act (MGVR) of 2014 led to an uptick in firearms sales ahead of the law. While
Balakrishna and Wilbur (2022) and Iwama and McDevitt (2021) find large increases in
firearm sales in response to stricter laws, the duration of their periods of the increase
are much shorter than in the case of Oregon’s Measure 114. Depetris-Chauvin (2015)
documents an increase in firearms sales following President Obama’s election in 2008.
While Depetris-Chauvin (2015) finds a long-term effect, Figures 10 and 14 suggest that
the increase due to Oregon’s Measure 114 is considerably larger than the "Obama Effect"
for Oregonians.
We offer several possible explanations for Measure 114’s unmatched effect
on firearm sales. First, in the cases of Balakrishna and Wilbur (2022) and Iwama and
McDevitt (2021), they do not proxy for firearm sales. Given that Massachusetts law, the
authors can take advantage of a direct measure of all firearm sales in the state. In contrast,
we must resort to background checks as a proxy for firearms sales. Consequently, our
measure of firearms sales could also be counting firearms-related background checks that
are not new firearms sales (e.g., background checks may be run for “concealed-carry”
permits). However, in our state-level analysis, we subset the FBI data to include just non-
private firearms sales, and in our OSP-FBI data comparison exercise (see Figure 7), we
find that the OSP data do not appear to include permit-related checks. It is also worth
noting that not every background check run made to support a possible firearms actually
sale results in a purchase, and some background checks can be shared across multiple
purchases by the same individual. An argument thus can be made that our proxy is just as
likely to undercount firearm sales as it is to overcount them.
Another possible explanation for Measure 114’s effect is that it was more salient
to individuals than the specific gun laws studied in other circumstances. Depetris-
Chauvin finds evidence for two competing explanations for increased firearms sales:
fear of firearms control, and racial prejudice. Importantly, an actual firearm control law
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motivated neither of these mechanisms. Unsurprisingly, the actual passage of a specific
firearms-related law is more salient to citizens than the fear of the election of a perceived
anti-firearm politician. In contrast to Depetris-Chauvin (2015), Balakrishna and Wilbur
(2022) and Iwama and McDevitt (2021) measure the impacts of actual firearm control
laws. However, again, an argument can be made that Measure 114 is more salient to
the affected citizens. Citizens did not have an opportunity to personally vote on the
firearm laws that Balakrishna and Wilbur and Iwama and McDevitt studied. Balakrishna
and Wilbur study an existing law that was unpredictably reinterpreted, and Iwama and
McDevitt study a law introduced and passed by the state legislature, not by statewide
referendum. Measure 114 is distinct from these laws because it began as a petition that
gained enough support to warrant its inclusion on Oregon’s 2022 election ballot and then
was voted on by Oregonians. Measure 114 was in the public eye for an extended period,
required citizen participation, and was sufficiently controversial to be only narrowly
approved by voters.
The difficulty in implementing Measure 114 after its passage might explain the
sustained surge in background checks. The ban studied by Balakrishna and Wilbur went
into effect within 24 hours of the state government’s announcement of the ban, and "[T]he
announcement was widely seen as a surprise. It was not preceded by public comment or
debate." This element of surprise may account for why Balakrishna and Wilbur found
no evidence of any anticipatory buying before the announcement, and following the
ban, firearm sales decreased well below the pre-ban rate. Iwama and McDevitt find that
Massachusetts’ Gun Violence Reduction Act (MGVR) of 2014 led to an uptick in firearm
sales ahead of the law. However, the authors find, "As anticipated, [the association
between the legislation passing and handgun sales] dissipated quickly over time." We
find no such quick dissipation. During the time since its passage in November 2022,
Measure 114 has been stuck in Oregon’s court system—challenged as violating the 2nd
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Amendment. As a result, Measure 114 inspired anticipatory firearms purchases but is, as
of this writing, still unable to increase firearms controls in the long run.
As a thought exercise, we estimate how long it would take for Measure 114’s
implementation to reverse the increase in firearms that it inadvertently induced. To do
this, first, we calculate the weekly rate of background checks for Oregon before the
“Measure 114” effect. We exclude the surge in background checks in March 2020 due
to the onset of the CoViD-19 pandemic. In the end, we calculate the mean for weekly
background checks in Oregon from February 2018 through September 2022 to be roughly
6,100 statewide checks. We then assume that the cumulative increase in firearm sales
resulting from Measure 114 ends in March of 2023—which is unlikely, given the trend
in the data. As indicated in Table 19, the cumulative increase is approximately 147,000
background checks. We then assume a reduction level in the case that Measure 114
was implemented. For the sake of argument, we choose an ambitious 20% reduction
in firearm sales. In this scenario, it would take approximately 120 weeks—over two
years—to achieve a cumulative reduction in firearms equivalent to the increase induced
by Measure 114. Of course, if we choose a more realistic reduction in firearm sales, the
timeline increases considerably.
After documenting the large surge in background checks in Oregon, we turned
to the task of disentangling this increase by examining heterogeneity across Oregon
counties. Measure 114 was a highly contested bill—winning less than 51% of the
popular vote. Most counties individually opposed the bill, which passed statewide due
only to support from those counties containing the large urban centers. We explore the
relationship between support for the bill and changes in background checks. In general,
smaller, rural, and right-leaning counties were responsible for about half of the increase in
background checks, despite making up only a small share of the state’s population. This
dynamic is consistent with work exploring the relationship between political ideology and
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firearm ownership (e.g., Burton et al., 2021; García-Montoya, Arjona, & Lacombe, 2022;
Joslyn, Haider-Markel, Baggs, & Bilbo, 2017; Tatalovich & Haider-Markel, 2022; Warner
& Ratcliff, 2021). Joslyn et al. (2017) argues that firearms ownership is becoming one
of the strongest correlates for Republican ideologies. Table 20 indicates that the greatest
per-capita increases in county-level background checks occurs in more-rural counties that
oppose Measure 114 (e.g., Harney, Douglas, Union, and Tillamook Counties). However,
there are several exceptions. For example, despite broadly supporting Measure 114
relative to other counties, Hood River saw one of the largest increases in background
checks. Lake County voted strongly against the law but saw only a relatively modest
increase in background checks. Part of the explanation for these contradictions could be
attributed to the very small populations in some Oregon counties, and using whole states
othe than Oregon to synthetically control for such small counties could lead to perplexing
results. It is also possible that the relationship between firearm ownership, support for
firearm control, and responses to imminent control is nuanced. While it is reasonably
straightforward to determine who owns a firearm, the psychology and social attitude
of firearm owners are complex (Burton et al., 2021; Schleimer et al., 2020). Panel 2 of
Figures 15 and 17 demonstrate that background checks increased the most in counties
with historically higher shares of background checks per capita. This result suggests that,
to some degree, a larger share of the increase in firearms sales can be attributed to people
or people with neighbors who already owned firearms before Measure 114.
It is unclear what will be the long-term impact of Measure 114 and related
Senate Bill 348 on firearms prevalence and overall welfare in Oregon. Measure 114
undoubtedly induced a substantial increase in firearm sales. Moreover, neither law
has been successfully implemented. A robust body of work demonstrates that firearm
ownership rates are often positively correlated with suicide and homicide rates (e.g.,
Braga, Griffiths, Sheppard, & Douglas, 2021; Cook & Donohue, 2017; Depetris-Chauvin,
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2015; Lang, 2013; Siegel & Rothman, 2016). Additionally, research finds examples of
stricter laws reducing suicide and homicide rates.7 A complementary body of work
suggests that laxer laws lead to increased rates of homicide and suicide.8 However,
reviews of the extant research find that the impact of firearms control laws is far from
conclusive (Santaella-Tenorio, Cerdá, Villaveces, & Galea, 2016; Wintemute, 2015,
2019).
The apparently variable impacts of firearms laws could be attributed to the
implementation and enforcement of these different laws (Wintemute, 2019). For instance,
there is evidence that individuals in states with Universal Background Check (UBC) laws
do not always get background checks (e.g., Hepburn et al., 2022; Kravitz-Wirtz et al.,
2021; Miller, Hepburn, & Azrael, 2017). Comparing the results of (Castillo-Carniglia
et al., 2018, 2019) Castillo-Carniglia (2018, 2019) and (Kagawa et al., 2023) provides
a good example of how non-compliance can obscure measurement of the efficacy of
laws. Castillo-Carniglia et al. found that while the states of Colorado, Delaware, Oregon,
and Washington passed UBC laws, background checks increased only in Delaware
and Oregon—suggesting non-compliance. Kagawa et al. found that UBC laws in
Colorado, Delaware, Oregon, and Washington do not unambiguously reduce suicide rates.
Considering the apparent non-compliance in Colorado and Washington, it is difficult
to know how to interpret Kagawa’s results. Balakrishna and Wilbur (2022) provide
another example of non-compliance. They find that the sale of banned firearms decreased
substantially after the ban, but did not decrease to zero.
7(e.g., Andrés & Hempstead, 2011; Anestis et al., 2015; Conner & Zhong, 2003; Cook & Ludwig, 2006;
Crifasi et al., 2018; G. Edwards, Nesson, Robinson, & Vars, 2018; Irvin, Rhodes, Cheney, & Wiebe, 2014;
Klarevas, Conner, & Hemenway, 2019; Knopov et al., 2019; G. Liu & Wiebe, 2019; Luca, Malhotra, &
Poliquin, 2017; McCourt et al., 2020; Raissian, 2016; Rudolph et al., 2015; Siegel, Pahn, Xuan, Fleegler,
& Hemenway, 2019; J. Smith & Spiegler, 2020; Tashiro, Lane, Blass, Perez, & Sola, 2016; D. W. Webster,
McCourt, Crifasi, Booty, & Stuart, 2020).
8(e.g., Alban et al., 2018; Donohue, 2017; Doucette, Crifasi, & Frattaroli, 2019; Fleegler, Lee,
Monuteaux, Hemenway, & Mannix, 2013; Reeping et al., 2022; Siegel et al., 2017; M. C. Williams, n.d.).
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In addition to non-compliance, the heterogeneity in state laws may undermine
the efficacy of state-level firearm control laws. Evidence shows that firearms tend to
flow from states with laxer laws into states with stricter laws (e.g., Andrade et al., 2020;
Knight, 2013; Takada et al., 2021). Concerningly, but perhaps not unsurprisingly, firearm
homicides are more often connected to illegally acquired firearms (e.g., Braga, Brunson,
Cook, Turchan, & Wade, 2021; Cook, 2018; Cook, Harris, Ludwig, & Pollack, 2015;
Semenza, Stansfield, Steidley, & Mancik, 2023).
Firearm violence is a "public health crisis" (Braga, 2022). Despite scattered
minimal increases in firearms control, support for firearms control continues to increase
(Crifasi et al., 2020). However, an effective way to reduce firearms violence through
state-level laws remains elusive. Relaxing firearm controls leads to increased firearms
sales, and tightening firearms controls—at least in the short run—also leads to increased
firearms sales. Measure 114 is thus a cautionary tale for policymakers: A firearm control
law will lead to an increase in firearms if it is not quickly and effectively passed and
meticulously enforced.
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4.7 Tables and Figures
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Table 17. Firearm laws in 2023
State-level background check, permit-to-purchase, and high capacity magazine laws in 2023.
Background Check Laws
State What type of guns require BGC? When is the background check performed? High capacity magazines prohibited? Permit-to-purchase law?
Alabama — — No —
Alaska — — No —
Arizona — — No —
Arkansas — — No —
California All firearms (handguns, rifles, and shotguns) Point-of-sale Yes —
Colorado All firearms (handguns, rifles, and shotguns) Point-of-sale Yes —
Connecticut All firearms (handguns, rifles, and shotguns) Permit to purchase and point-of-sale Yes Yes
Delaware All firearms (handguns, rifles, and shotguns) Point-of-sale Yes —
Florida — — No —
Georgia — — No —
Hawaii All firearms (handguns, rifles, and shotguns) Permit to purchase Yes Yes
Idaho — — No —
Illinois All firearms (handguns, rifles, and shotguns) Permit to purchase and point-of-sale Yes Yes
Indiana — — No —
Iowa — — No —
Kansas — — No —
Kentucky — — No —
Louisiana — — No —
Maine — — No —
Continued on next page
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Table 17 – continued from previous page
Maryland All firearms (handguns, rifles, and shotguns) Permit to purchase (for handguns) Yes Yes
and point-of-sale (for all guns)
Massachusetts All firearms (handguns, rifles, and shotguns) Permit to purchase Yes Yes
Michigan All firearms (handguns, rifles, and shotguns) Permit to purchase No Yes
Minnesota Handguns Permit to purchase or point-of-sale No Optional
and semiautomatic military-style assault weapons
Mississippi — — No —
Missouri — — No Repealed
Montana — — No —
Nebraska Handguns only Permit to purchase No Repealed
Nevada All firearms (handguns, rifles, and shotguns) Point-of-sale No —
New Hampshire — — No —
New Jersey All firearms (handguns, rifles, and shotguns) Permit to purchase and point-of-sale Yes Yes
New Mexico All firearms (handguns, rifles, and shotguns) Point-of-sale No —
New York All firearms (handguns, rifles, and shotguns) Permit to purchase (for handguns and semiautomatic rifles) Yes Yes
and point-of-sale (for all guns)
North Carolina — — No Repealed
North Dakota — — No —
Ohio — — No —
Oklahoma — — No —
Oregon All firearms (handguns, rifles, and shotguns) Permit to purchase and point-of-sale Yes Yes
Pennsylvania Handguns only Point-of-sale No —
Rhode Island All firearms (handguns, rifles, and shotguns) Point-of-sale Yes Yes
South Carolina — — No —
South Dakota — — No —
Continued on next page
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Table 17 – continued from previous page
Tennessee — — No —
Texas — — No —
Utah — — No —
Vermont All firearms (handguns, rifles, and shotguns) Point-of-sale Yes —
Virginia All firearms (handguns, rifles, and shotguns) Point-of-sale No —
Washington All firearms (handguns, rifles, and shotguns) Point-of-sale Yes —
West Virginia — — No —
Wisconsin — — No —
Wyoming — — No —
Table 18. Change in Oregon Background Checks after Measure 114
Type of Check Estimate S.E. CI.lower CI.upper P.value
Raw Count
Handgun 21,500 1,800 18,000 25,000 <0.001
Long gun 7,700 1,600 4,600 10,800 <0.001
All non-private gun sales 28,700 2,800 23,300 34,100 <0.001
Per 100,000 residents
Handgun 516 25 466 566 <0.001
Long gun 178 26 127 229 <0.001
Non-private gun sales 679 45 591 767 <0.001
Notes: Results from synthetic control difference-in-difference. Estimated
using state-level FBI background checks from January, 2000 through March,
2023. Treatment spans from Nov. 2022 through Feb. 2023.
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Table 19. Cummulative change in Oregon Background Checks after Measure 114
Type of Check Months after election Estimate S.E. CI.lower CI.upper P.value
Raw Count
Handgun 0 (Oct. 2022) 3,500 1,700 300 7,900 0.048
1 (Nov. 2022) 45,300 3,300 39,400 52,500 <0.001
2 (Dec. 2022) 72,800 5,400 61,400 84,600 <0.001
3 (Jan. 2023) 89,400 6,800 75,600 104,100 <0.001
4 (Feb. 2023) 97,800 8,600 79,300 115,700 <0.001
5 (Mar. 2023) 111,100 10,200 92,500 134,900 <0.001
Long gun 0 300 16,00 -3,100 3,000 0.628
1 16,000 3,100 8,700 20,900 0.012
2 24,700 5,100 12,500 33,000 0.012
3 30,400 6,500 13,800 41,300 0.014
4 32,900 7,700 13,900 45,500 0.016
5 38,700 9,100 14,700 54,300 0.016
Non-private gun sales 0 3,700 2,200 -1,300 8,300 0.098
1 60,900 4,300 51,300 68,800 <0.001
2 96,600 7,100 81,100 110,900 <0.001
3 118,400 9,200 99,500 138,000 <0.001
4 129,200 11,200 107,100 154,000 <0.001
5 147,300 14,600 113,200 177,400 <0.001
Per 100,000 residents
Handgun 0 93 21 55 140 <0.001
1 1,079 48 990 1,192 <0.001
2 1,731 81 1,575 1,912 <0.001
3 2,143 101 1,941 2,376 <0.001
4 2,349 124 2,095 2,635 <0.001
5 26,73 145 2,392 3,013 <0.001
Long gun 0 -5 23 -51 46 0.906
1 362 49 253 468 <0.001
2 555 83 389 764 <0.001
3 695 106 488 961 <0.001
4 749 129 485 1,054 <0.001
5 883 149 580 1,206 <0.001
Non-private gun sales 0 84 38 14 166 0.020
1 1,427 81 1,259 1,610 <0.001
2 2,258 135 1,972 2,561 <0.001
3 2,792 172 2,437 3,180 <0.001
4 3,039 213 2,591 3,515 <0.001
5 3,479 252 2,960 4,036 <0.001
Notes: Results from synthetic control difference-in-difference. Estimated using state-level FBI
background checks from January, 2000 through March, 2023. Treatment spans from Nov. 2022
through Feb. 2023.
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Table 20. County-level changes in Oregon Background Checks after Measure 114
County Estimate S.E. CI.lower CI.upper p.value
Baker 604.11 77.85 451.54 756.69 <0.001
Benton 293.05 46.07 202.76 383.34 <0.001
Clackamas 492.04 53.13 387.91 596.17 <0.001
Clatsop 290.70 45.87 200.79 380.60 <0.001
Columbia 644.16 53.13 540.04 748.29 <0.001
Coos 542.44 49.20 446.01 638.88 <0.001
Crook 567.42 56.92 455.86 678.98 <0.001
Curry 164.10 55.49 55.35 272.85 0.003
Deschutes 516.09 55.10 408.09 624.09 <0.001
Douglas 872.43 57.85 759.05 985.81 <0.001
Gilliam 286.34 56.27 176.05 396.63 <0.001
Grant 583.12 53.13 478.99 687.25 <0.001
Harney 1194.93 74.14 1049.61 1340.24 <0.001
Hood River 901.86 47.56 808.64 995.08 <0.001
Jackson 519.09 55.84 409.65 628.53 <0.001
Jefferson 238.37 53.19 134.13 342.62 <0.001
Josephine 464.66 54.97 356.91 572.40 <0.001
Klamath 539.01 50.77 439.50 638.52 <0.001
Lake 152.73 48.21 58.24 247.21 0.002
Lane 473.86 53.13 369.73 577.99 <0.001
Lincoln 578.81 48.00 484.73 672.88 <0.001
Linn 725.99 50.73 626.57 825.41 <0.001
Malheur -4.99 64.11 -130.65 120.66 0.938
Marion 620.44 54.65 513.33 727.56 <0.001
Morrow 174.87 52.16 72.65 277.09 0.001
Multnomah 164.59 55.31 56.19 273.00 0.003
Polk 264.62 42.28 181.75 347.49 <0.001
Sherman 581.36 55.78 472.04 690.69 <0.001
Tillamook 754.47 50.41 655.66 853.27 <0.001
Umatilla 545.84 49.04 449.71 641.96 <0.001
Union 759.19 56.22 649.00 869.38 <0.001
Wallowa 655.54 68.11 522.05 789.03 <0.001
Wasco 397.37 57.28 285.09 509.64 <0.001
Washington 368.40 53.13 264.27 472.53 <0.001
Wheeler -58.01 45.64 -147.46 31.43 0.204
Yamhill 735.33 54.49 628.53 842.12 <0.001
Notes: Results from synthetic control difference-in-difference.
Treatment is for individual Oregon counties from Feb. 2018
through Feb. 2023. Controls estimated using state-level FBI
background checks.
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134
Figure 7. FBI vs. OSP data
Comparing OSP data to different subsets of FBI data suggests that excluding permit-related background checks from the FBI
data gives the closest match between datasets. Non-private gun sales is compromised of handgun, long gun, other, and multiple
from the FBI data. Non-permit excludes permit and permit-recheck from the FBI data.
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Figure 8. Google Trends search for Measure 114
We use Google Trends to examine Oregonians’ awareness of Measure 114. The observation period is from January of 2022
until April 2023. Google Trends observations are at the week level. The search index is calculated that the week with the highest
number of searches in the obersation period is 100, and all other weeks are normalized to that week.
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Figure 9. Synthetic control difference-in-difference for Oregon background checks (per
capita)
Background check data is Non-private gun sales subset of FBI data. Outcome variable, background checks, calculated as a per
capita (100,000 state residents). The top panel confirms previous findings that Mass-shooting Events and fear of gun control that
led to changes in gun purchasing behavior (e.g., Obama’s election in 2008).
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Figure 10. Weekly timeseries (2018-2022)
Background checks provided by Oregon State Police from Feb. 2018 through Feb. 2023. Data has been aggregated from the
daily level to weekly checks. There are two significant spikes in checks: Covid lockdown begins and Measure 114 passes.
138
Figure 11. Weekly timeseries (2022)
Background checks provided by Oregon State Police from Jan. 2022 through Feb. 2023. Data has been aggregated from the daily
level to weekly checks. Anticipatory behavior appears to begin in October (marked in red). Increased sales persist through mid-
January (marked in blue).
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Figure 12. Daily timeseries
Background checks provided by Oregon State Police from Aug. 2022 through Feb. 2023. Sunday and Monday of each week were
dropped to improve interpretability. Anticipatory behavior appears to begin in October (marked in red). Increased sales persist
through mid-January (marked in blue). The highest number of background checks are recorded on “Black Friday.” There were a
significant number of background checks ( 2000) recorded on 12/13 and 12/14 but were attributed to an “Unknown” county and
were dropped. Background checks decreased significantly near and on Christmas.
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Figure 13. Event Study for OSP background checks (11-08)
Background checks aggregated to the week. Event date is the week of Election Day (11/08). Point of reference: 11-08-22. We see
consistently statistically significant negative observations preceding our event date, suggesting that background checks increased
before our event date.
141
Figure 14. Event Study for OSP background checks (10-2)
Background checks aggregated to the week. Event date is the week of (10/10). Point of reference: 10-02-22. We see consistently
statistically significant negative observations preceding our event date, suggesting that background checks increased before our
event date.
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Figure 15. Timeseries for by majority vote share (2018-2022)
Background checks aggregated to the week. Background checks are separated into two groups: counties that voted in majority
for Measure 114 (blue) and counties that voted in majority against Measure 114 (red). The top panel measure total checks and
the bottom panel measures checks per capita (100,000 residents).
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Figure 16. Timeseries by majority vote share (2022)
Background checks aggregated to the week. Background checks are separated into two groups: counties that voted in majority
for Measure 114 (blue) and counties that voted in majority against Measure 114 (red). The top panel measure total checks and
the bottom panel measures checks per capita (100,000 residents).
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Figure 17. Timeseries by quartile vote share (2018-2022)
Background checks aggregated to the week. Background checks are separated into quartiles (9 counties per quartile). Quartile
is decided by votes for Measure 114. The first quartile for support for Measure 114 is [11%, 20.8%], the second quartile is
(20.8%, 31%), the third quartile is (31%, 43.5%], and the fourth quartile is (43.5%, 74%]. The top panel measure total checks
and the bottom panel measures checks per capita (100,000 residents).
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Figure 18. Timeseries by quartile vote share (2022)
Background checks aggregated to the week. Background checks are separated into quartiles (9 counties per quartile). Quartile
is decided by votes for Measure 114. The first quartile for support for Measure 114 is [11%, 20.8%], the second quartile is
(20.8%, 31%), the third quartile is (31%, 43.5%], and the fourth quartile is (43.5%, 74%]. The top panel measure total checks
and the bottom panel measures checks per capita (100,000 residents).
CHAPTER V
CONCLUSION
In this dissertation, I examine public goods in three contexts: local law
enforcement behavior, climate change policy, and firearms control laws. I find that
while public goods are designed to improve social welfare, the presence of heterogenous
agents can lead to inequitable and unintended outcomes. In each context, I use a different
methodological approach to identify some critical information needed to facilitate optimal
provision of these public goods.
In Chapter 2, I describe an audit study of local law enforcement agencies,
designed to test for racial/ethnic and gender bias. I find causal evidence that local law
enforcement agencies are substantially less likely to respond to requests from Black and
Hispanic citizens who ask for help making a complaint against an officer. Interacting the
race/ethnicity and gender of the requester provides even more insight into the disparate
treatment individuals receive, on average, from law enforcement. White males are the
most likely to receive assistance, and Black and Hispanic males are the least likely. The
results from this study may help to explain the great disparity in relations between law
enforcement and the different types of communities they serve. The results also indicate
that accountability, in general may be an essential area of improvement for may law
enforcement agencies in the United States.
Chapter 3 uses a choice experiment to identify individuals’ preferences for a state-
level carbon cap-and-trade program. Our survey design allows us to measure identify
different dimensions of heterogeneity in preferences. We find that sociodemographic
and ideological characteristics influence attitudes toward cap-and-trade programs and
their many possible configurations. Among the various characteristics we examine, an
individual’s attitude toward climate change is the strongest indicator of support for a
program. Successful adoption of effective climate change policy may hinge on improving
146
society’s understanding of climate change. We also undertake an exercise in benefit-
function transfer, exploiting heterogeneity in preferences across our representative
sample of Oregonians. We explore the implications of our study for cap-and-trade
program preferences at national level, as a function of heterogeneous local community
characteristics across the rest of the United States.
Finally, Chapter 4 examines the impact of Oregon’s recently passed firearms
control law. We find a record increase in firearms purchased by Oregonians in response
to the law. The intent of the law was to reduce firearms in the community, but the
combination of forward-looking agents and the halted implementation of the law may
have led to the opposite outcome. We christen this unintended effect the “Steel Paradox”
after the well-known “Green Paradox” in environmental economics. The “Steel Paradox”
is a cautionary tale for policymakers seeking to address the growing firearms crisis in the
United States.
147
APPENDIX A
CHAPTER 2 APPENDIX
A.1 Appendix: Police Department Selection
The selection process for police departments to be included in the study is as
follows:
1. From the universe of governments provided by the U.S. Census, I create a list
of possible jurisdictions that may have their own police departments. This list
excludes state governments, counties, special districts and places with populations
less than 7,500.
2. From the “possible department” list, I randomly a draw 1,000 jurisdiction names.
The target number of departments is 2,000, but to streamline the process, I select
possible department cities in 3 batches of 1,000. For each batch of jurisdictions,
roughly 60% have a viable police department, police chief or alternate email
addresses.
3. Email addresses are then collected from police department websites in these
jurisdictions.
– Governments without local police departments are dropped.
– Police departments without publicly available email addresses are documented
and dropped.
– In the cases where there are multiple email addresses the prioritization is
given first to (1) the email address for the department in general, and then
to (2) the email address specifically for the police chief, (3) and finally to any
possible contact (e.g., a community-affairs officer). I document the type of
email address ultimately recorded in my database.
148
4. I repeat Steps 2 and 3 until 2,000 email addresses have been collected. Given that
jurisdictions are selected in batches of 1,000, the final number of police department
emails collected is 2,135.
Randomization of the department selection process increases the external validity
of the study. Requiring that populations served by these police departments are greater
than 7,500 increases the plausibility of the existence of the purported email sender as a
resident of their jurisdiction.
A.1.1 Type of email collected. During the police department email address
collection, the “type” of email address publicly available for collection varied from
department to department. In this case, “type” refers to who is associated with the email
address. For example, for Department X the only publicly available email address is
for the chief of that department and for Department Y the only publicly available email
address is for the shift-commander. In this example, I collect the email address for each
department, and record that the email address type for Department X is chief and the
email address type for Department Y is shift-commander. During the actual department
email address collection, frequently departments had multiple email addresses publicly
available.1 In the case of the existence of multiple publicly available email addresses, I
used a consistent priority list to decide which email address to collect. Prioritization is as
follows:
1. Top priority is given to a general department email address. This is done to get the
most accurate representation of a department’s general behavior.
2. In the absence of a general department email address, priority is given to the chief
of police.
1In other instances, there were no publicly available email addresses associated with a police department
of interest.
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3. In the absence of a general department email address or a chief email address,
priority is given to the next highest in command officer.
4. In the absence of (1) (2) and (3), the email address for the records department is
collected.
5. If none of the above email addresses are publicly available, any email address
available on the the police department website is collected.
6. If there are no email addresses available on the department website, a cursory
search is performed to find email contacts on other related websites (e.g., the
website of the city that a department is located in or the official Facebook page
for a department)
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A.2 Appendix: Identity Construction
Six different “identities” are used in this study:
1. Black Female
2. Black Male
3. White Female
4. White Male
5. Hispanic Female
6. Hispanic Male
Consistent with standard practices in the correspondence study literature, identity
(gender and race/ethnicity) of the email sender will be implied by name (first name and
last name). Ten unique first names and six unique last names are chosen for each identity
(60 unique name combinations for each identity). Using multiple names for each identity
minimizes the importance of a specific name.
– First names are selected from research done by Gaddis (Gaddis (2017a), Gaddis
(2017b)). The top ten most racially identifiable first names (when coupled with last
names), are chosen.
– Last names are selected from the 2010 Census. Three criteria are used to select last
names:
1. Percent of persons with that name having a specific race/ethnicity (e.g., White)
2. Percent of persons with that name having the other relevant race/ethnicity
(e.g., Black or Hispanic)
3. The rank of the name (i.e. how common the last name is in the United States)
151
Name Search Equation: I selected surnames for this experiment that were both (1)
racially distinctive and (2) commonly found. Priority was given to racially distinctive,
because of the importance of race in the design of the experiment. However, I also wanted
to avoid the scenario where police departments act differently if they see an exceedingly
uncommon last name. In other words, I want race, and only race, to be communicated by
the name of the identity. The three equations below reflect the priorities I used to select
the names. I decided it was unnecessary to difference the Hispanic surnames with the
other two groups because of how uncommon it was for Black and White people to have a
surname commonly used by Hispanic people.
– For Black Names: percent raceblack − percent racewhite)− .05× rankblack name
– For White Names: percent racewhite − percent raceblack)− .05× rankwhite name
– For Hispanic Names: percent racehispanic − .05× rankwhite name
The full list of names can be inferred by the following two tables (there are 360
unique name combinations). Six high-profile recognizable celebrity names were omitted:
Denzel Washington, Tyra Banks, DaShawn Jackson, Seth Meyer(s), Katelyn Olson and
Pedro Martinez. These names have widespread recognition and during the testing process,
respondents noted that they strongly associate these names with the celebrities having the
same name.
152
Last Names
White Black Hispanic
Olson Washington Hernandez
Schmidt Jefferson Gonzalez
Meyer Jackson Rodriguez
Snyder Joseph Ramirez
Hansen Williams Martinez
Larson Banks Lopez
First Names
White Male White Female Black Male Black Female Hispanic Male Hispanic Female
Hunter Katelyn DaShawn Tanisha Alejandro Mariana
Jake Claire Tremayne Lakisha Pedro Guadalupe
Seth Laurie Jamal Janae Santiago Isabella
Zachary Stephanie DaQuan Tamika Luis Esmeralda
Todd Abigail DeAndre Latoya Esteban Jimena
Matthew Megan Tyrone Tyra Pablo Alejandra
Logan Kristen Keyshawn Ebony Rodrigo Valeria
Ryan Emily Denzel Denisha Felipe Lucia
Dustin Sarah Latrell Taniya Juan Florencia
Brett Molly Jayvon Heaven Fernando Juanita
As mentioned, the first names were selected from Gaddis (2017a) and Gaddis
(2017b). In these studies, Gaddis analyzes the correlation between the average level of the
mother’s education for a given first name and accuracy of perceived race and ethnicity of
that name. For instance, Black names associated with lower education levels for mothers
are more often perceived as Black than Black names associated with mothers with
153
higher average education levels. In my study, while creating the identities, the associated
maternal education levels documented by Gaddis are recorded in my database.
154
A.3 Appendix: Email Account Creation
To implement this study, sender email addresses had to be created for each
putative identity. Ideally, each of the 360 identities would have a unique email address.
During the pre-testing process, respondents suggested that
“firstname.lastname.birthyear@mail.com” was the most realistic email address
template. However, due to constraints from popular email servers (e.g., Yahoo), this
was not feasible. Instead, a unique account was made for each last name (18 accounts
in total). Due to availability, I had to be creative in creation of the email address. All of
the addresses include some version of the relevant last name.
Due to the prevalence of people with the last names chosen for the study, it
was often difficult to find available addresses with the specific last name. As a result,
I had to make creative decisions to create a plausible and name-relevant address.
For example, “h3rnandez.1973@mail.com”. Often included is a birth year (e.g.,
Banksss.1991@mail.com).
155
A.4 Appendix: Example Email
A.4.1 Email Text. The body of text for the email has been developed in
consultation with other economists and a legal expert. The primary criterion in creating
the right text for these emails concerned plausibility—i.e., I needed to create an email
that sounded like a genuine request from a real citizen. Drafts of the email were sent to
colleagues and police departments not selected for the correspondence study to assess the
plausibility of the email. The body of the email message template reads as follows:
Police Department Name,
My name is first name and I am interested in filing a complaint against
an officer in your department. I am not sure what to do, and would like to
request information on how to make a complaint. Can you please send me
this information?
sign off
full name
Where full name includes a first and last name, and sign off is randomly assigned as
“Thank you!” or “Sincerely,”. The decision to exclude a “Hi” or “Hello” was based on
the increased likelihood of the email being filtered as spam during the preliminary testing
process mentioned above. 2
2There is a small concern about this email being rejected as implausible. For example, a very small
police department might know everyone with whom they have recently interacted and would be able
to deduce, with little effort, that the email is fabricated. A small police department might also be more
likely not to respond to an email because of staffing limitations. However, because assignment of treatment
(see below) is balanced across departments, estimates should be remain unbiased. In future research, an
alternative email to departments with a more innocuous inquiry (e.g., “Do you have a lost-and-found?”)
could shed light on the matter.
156
Figure B1. Example email
Figure B2. Example email
157
A.5 Appendix: Treatment Assignment
Police departments are randomly assigned the sender identity they will see.
The first step of treatment assignment was to balance the number of departments by
state each week, so that every state received roughly the same number of emails each
week. Next race and gender treatment are randomly assigned within state, with race
and gender treatment levels balanced within each state. Given that assignment of emails
to department by week within state was randomized, race and gender assignments are
independent of week. Additionally, race and gender are roughly balanced across weeks—
also as a result of the randomization of all treatment components. After week, gender and
race are assigned, day of week is randomly assigned. Next, the sign off for each email is
randomly assigned (the email sign off can be either “Thank you” or “Sincerely” followed
by the sender’s name). The actual assignment of email sender first and last names to each
department is randomized across all weeks and states.
158
159
Table B1. Distribution of Race, Ethnicity and Gender identity assignment by state
State Putative Identities Response Statistics
State Black White Hispanic Male Female Total Mean
AK 3 2 2 4 3 5 0.714
AL 5 5 5 8 7 10 0.667
AR 6 4 6 7 9 8 0.500
AZ 6 5 4 9 6 12 0.800
CA 26 22 19 38 29 46 0.687
CO 7 7 5 10 9 14 0.737
CT 11 9 16 20 16 21 0.583
DE 2 1 1 1 3 2 0.500
FL 17 19 18 30 24 35 0.648
GA 9 10 6 10 15 14 0.560
IA 6 6 4 5 11 6 0.375
ID 3 3 5 6 5 6 0.545
IL 28 26 29 39 44 61 0.735
IN 10 10 11 16 15 19 0.613
KS 5 7 6 11 7 11 0.611
KY 3 5 4 7 5 6 0.500
LA 2 6 4 7 5 6 0.500
MA 16 17 19 28 24 31 0.596
MD 7 5 2 8 6 7 0.500
ME 6 5 6 8 9 10 0.588
MI 14 18 12 22 22 27 0.614
MN 12 8 11 13 18 24 0.774
MO 9 9 10 16 12 16 0.571
MS 6 5 5 7 9 4 0.250
MT 2 1 3 1 5 3 0.500
NC 10 6 11 12 15 17 0.630
ND 3 1 1 2 3 4 0.800
NE 4 6 2 5 7 10 0.833
NH 4 4 6 7 7 9 0.643
NJ 27 30 25 41 41 45 0.549
NM 5 3 4 7 5 3 0.250
NV 2 1 2 3 2 2 0.400
NY 14 18 19 26 25 31 0.608
OH 25 21 32 37 41 49 0.628
OK 6 7 3 8 8 10 0.625
OR 7 6 10 10 13 17 0.739
PA 25 22 21 33 35 44 0.647
RI 3 3 4 4 6 5 0.500
SC 5 6 4 10 5 7 0.467
SD 1 3 1 3 2 4 0.800
TN 6 6 6 10 8 12 0.667
TX 31 20 31 41 41 60 0.732
UT 6 4 2 8 4 9 0.750
VA 6 3 3 6 6 8 0.667
VT 2 3 3 3 5 6 0.750
WA 11 9 9 13 16 20 0.690
WI 10 10 11 17 14 26 0.839
WV 3 4 4 1670 4 4 0.364
WY 1 2 3 4 2 4 0.667
Figure B3. Emails sent by week.
161
Figure B4. Departments by state included in the study.
162
Table B2. Distribution of Race, Ethnicity and Gender identity assignment by week
Week Putative Identities Response Statistics
week Black White Hispanic Male Female Total Mean
1 75 73 68 107 109 139 0.644
2 74 79 63 103 113 141 0.653
3 59 68 77 103 101 132 0.647
4 74 60 76 119 91 123 0.586
5 77 62 78 104 113 144 0.664
6 79 71 68 112 106 131 0.601
A.6 Appendix: Experiment Implementation
I created eighteen email accounts—one for each last name. The accounts were
then linked to Mozilla’s Thunderbird mail application to help automate the emailing
process.3 In Thunderbird, for each email address, 20 identities were created (10 females
and 10 males). Although the email address that is seen by police departments cannot
be arbitrarily manipulated, the “name” of the sender can be changed from message to
message. For instance, an email can be sent as Claire Olson <olson2292@mail.com> or
Hunter Olson <olson2292@mail.com>. This helps increase the salience of the putative
identity and decrease attention to the less-specifc email address itself.
Each department will receive just one email. Emails will be sent over a ten-week
period. Spreading out the randomized controlled trial (RCT) over 10 weeks insures
against the possibility that unique unanticipated current events could plausibly affect
police department behavior (e.g.„ a high-profile regional or national incident involving the
police). In the case of a high-profile policing incident, a weekly roll-out of the emails will
3I had originally intended to use the mailR package from R, but due to increased security policies with
many popular email servers, that option is no longer as user friendly. To use mailR with, for example,
Google, one needs to change the Google account settings to allow “less secure apps”. However, as of May
31st, this setting can no longer be adjusted. There are possible workarounds, but I decided to adopt an
alternate strategy.
163
allow me to detect the possible effect of any such event on police departments’ responses
to the emails.
The timing of the roll-out is randomly selected using the following procedure.
Police departments are randomly assigned to one of the ten weeks, while being stratified
proportional to the total number of departments in each state. Each state’s total police
departments (in my data set) are split into 10 equal groups and assigned to a week. In
the event that, after the initial assignment, the number of departments by state are not
divisible by 10, the remainder of the police departments are randomly assigned across
the weeks. In the event that the total number of departments from a state is less than 10,
departments are randomly assigned to the ten different weeks (with a maximum of one
department per week). Each putative sender identity (i.e. email address) has the same
probability of being assigned to any one of the 10 weeks.
During each week, the emails are sent on Monday, Tuesday and Wednesday.
Assignment of weekday is randomized. The decision to choose different days is largely
motivated by an effort to improve the ease of implementation of the emailing process for
the researcher. Each email must be sent individually, so it proved easier for me to monitor
the email process by spreading out the emails over a few days (with roughly 70 emails
being sent each day).
All emails are sent at roughly 9 a.m. local time according to the time zone of the
police department in question. However, if for a given week and given day, the same
email sender address is being used for more than one police department (as dictated by
the random assignment of race), a five-minute delay between each email from the same
address, independent of first name, is employed. The strategy is adopted so that a single
putative email account does not have to send more than one email at an exact time (i.e. at
exactly 9 a.m.).
164
A.7 Appendix: Response Time and Word Count
Not all responses are created equally: The current analysis of the data from this
correspondence study designates the outcome variable to be a police department’s timely
non-automated response to a request for help. Consequently, the results are a coarse
reflection of the average department’s willingness to respond to a citizen’s request for
help in making a complaint about an officer. However, the premise of biased policing
refers to both the frequency of interaction between officers and citizens, as well as the
conduct during the interaction. Even in the specific context of an email request for a
complaint form, detecting and understanding potential differences in department behavior
across different sender identities is worth exploring. For example, conditional on a
department providing any response, do responses differ in their helpfulness and tone
across identities and, if so, how do they differ? In some instances, scrutiny of verbatim
department responses reveals that not all departments are willing to guide the citizen to
the officer-complaint forms. In other instances, departments specifically advise against
making a formal complaint. Responses also tend to reflect a wide range of sentiment.
Some departments include an apology on behalf of the department, while others simply
send a phone number with no other information—the assumed implication being that
the complainant should call that number for assistance. To begin to answer the question
of differential response conditional response, a cursory examination of heterogeneity of
responses is performed.
Table B3 reports the differentials of (1) the word count of emails from the
departments and (2) the time it takes for a department respond between White male
identities and the other five identities. Table B3 suggests that conditional on response,
at least on the two specified dimensions, there does not seem to be any evidence of
discrimination. There are a few reasons to not make strong conclusions about these null
results. Most importantly, the analysis is subject to selection bias. These results are based
165
Table B3. Response time and word count of response measured across identities
Dependent Variables: Word Count Response Time (hours)
Model: (1) (2)
Variables
White × Female 0.2948 -1.653
(3.844) (2.573)
Hispanic × Male 3.909 3.032
(2.533) (3.103)
Hispanic × Female -3.051 -4.157
(3.937) (3.056)
Black × Male 4.518 8.778
(7.728) (7.215)
Black × Female -4.038 2.567
(2.849) (3.919)
Fixed-effects
Week Yes Yes
State Yes Yes
Fit statistics
Observations 1,413 1,413
R2 0.08298 0.04623
Within R2 0.00291 0.00892
Clustered (week & dept_address_state) standard-errors in
parentheses
Signif. Codes: ***: 0.01, **: 0.05, *: 0.1
166
only on the departments that do respond, which are different than the departments that do
not respond. Additionally, word count is a crude measure of helpfulness and sentiment.
An email could be helpful, friendly and to the point, but still would reflect a word count
similar to an email that is unhelpful and/or unfriendly. Time of response is a stronger
indicator of helpfulness. However, a quick response could be the result of a department
eager to help or a department being reactive to an accusation against one of their officers.
To get a strong understanding of differences in the helpfulness and sentiment of responses
would require selection correction and a more rigorous sentiment analysis.
167
A.8 Appendix: Summary Statistics
Figure B5 and B6 depict the average response time for identities by week. The
general average response time (66%) is depicted by the dotted black line. Reassuringly,
no week in particular seems to drive the results
Figure B5. Mean response rate by week by identities
1.0
0.9
0.8
0.7
0.6
0.5
0.4
1 2 3 4 5 6 7 8 9 10
Week email was sent
The mean response rate by week. Mean response rate across all weeks and identities
(66%) is depicted by dotted black line.
168
Response rate
169
Figure B6. Mean response rate by week for all putative identities
Black female Black male
1.0
0.9
0.8
0.7
0.6
0.5
0.4
Hispanic female Hispanic male
1.0
0.9
0.8
0.7
0.6
0.5
0.4
White female White male
1.0
0.9
0.8
0.7
0.6
0.5
0.4
1 2 3 4 5 6 7 8 9 10 1 2 3 4 5 6 7 8 9 10
Week email was sent
The mean response rate by week for all putative identities. Mean response rate across all weeks and identities (66%) is depicted
by dotted black line.
R e s p o n s e r a t e
Response Rate differential from White grouped by local population size
Group population size: 1 = [0 : 9,626], 2 = [9,632 : 14,188], 3 = [14,196 : 23,658], 4 = [23,663 : 47,408], 5 = [47,422 : 3,982,885]
0.05
0.00
-0.05 Putative Identity
Black
-0.10
Hispanic
-0.15
-0.20
-0.25
1 2 3 4 5
Figure B7. Response rates differentials by local population size
Response rates differentials for Black and Hispanic identities from White identities
separated into bins determined by local population size.
Comparing Columns 1 and 2 in Table 7 it is apparent that weighting by the
population of the police department’s jurisdiction exacerbates the differences in
response rates (with the exception of Hispanic male response rates). One possible
explanation for these results is that departments serving larger populations are more
likely to discriminate. To test this interpretation, departments are separated into five bins
determined by the quintiles of the local populations of the departments included in the
study. Model 1 from 6 is re-estimated, but this time interacting both Hispanic and Black
with the five population bins. Figure B7 shows the results of this exercise. Figure B7
reveals no clear pattern in the relationship between population size and response rate.
Black identity response rates are lowest for the largest and smallest quintiles, but the
pattern does not hold for Hispanic identity response rates.
The relationship between police department local population and response rate is
ambiguous. Notwithstanding a clear relationship between local population and propensity
170
to discriminate, heterogeneous response rates across population sizes suggest that studies
that restrict their area of focus to a limited number of local governments, or at least
similarly sized populations, may not be able to extend their results to smaller (or larger)
populations. Furthermore, the higher differentials in response rates between White and
non-White response rates when weighting by population (Table 7) indicate, in a crude
measure, that more people are discriminated against than is evident by finding the level of
discrimination for the average police department.4
A variable strongly correlated with local population size is the number of
employees working for a police department. Mechanically, as local populations increase,
so do the sizes of departments. For the departments include in the present study there
are on average 3 employees for every 1,000 residents. Results from Table 8 suggest that
bigger departments are more likely to discriminate against Black identities and White
female identities, and discriminate less against Hispanic identities. When the results are
weighted by population in Columns 3 and 4 in 8, the discrepancies grow, which makes
sense given that agency size is correlated with population size.5 To disentangle the effect
of agency size and population size on response rate given their the two sizes correlations,
the same exercise from Figure B7 is done. This time the quintiles are determined by the
number of employees divided by local population size—a per capita measurement. Figure
B8 displays the results of this exercise.
No clear pattern emerges for Hispanic or Black identity response rates. Compared
to Figure B7, Figure B8 has smaller differences for the first bin. However, in both figures
4The design of this study only sends one email to each department, so a department responding to a
White email does not necessarily mean the same department would not respond to a non-White email.
Conversely, a department not responding to a non-White email does not necessarily mean the same
department would respond to a White email. However, higher levels of discrimination for departments
serving larger populations do suggest that a larger share of the population might be discriminated against
than is indicated by the unweighted results.
5One curious result of Table 8 is comparing the point estimate for Hispanic females from Column 2 and
Column 4.
171
Response Rate differential from White grouped by dept. employee per 1,000 residents
Group population size: 1 = [0 : 1.66], 2 = [1.66 : 2.03], 3 = [2.03 : 2.41], 4 = [2.42 : 2.95], 5 = [2.95 : 15.7]
0.05
0.00
Putative Identity
-0.05
Black
-0.10
Hispanic
-0.15
-0.20
-0.25
1 2 3 4 5
Figure B8. Response rates differentials by local department size
Response rates differentials for Black and Hispanic identities from White identities
separated into bins determined by local department size.
the biggest bin, bin 5, exhibits large differences for Hispanic and Black response rates.
It is conceivable that the low response rates for departments with big populations might
be attributed to departments being overextended and thus less capable of responding to
requests for assistance. However, the highest employee per capita departments exhibiting
the highest degree of discrimination runs counter to that argument. It is concerning that
departments most capable, in terms of employees per capita, to respond to requests are
most likely to discriminate.
172
APPENDIX B
CHAPTER 3 APPENDIX
173
B.1 Appendix: Expanded Discussion of the Related Literature
B.1.1 Context. While the United States has yet to adopt a federal carbon
cap-and-trade program, regional carbon cap-and-trade programs have been adopted
(Schmalensee and Stavins (2017)). Federal inaction may necessitate that regional
coalitions and states to implement policies (Fullerton and Karney (2018); Peterson
and Rose (2006)). Recently, Oregon attempted twice to adopt a carbon cap-and-trade
program. In June of 2019, Oregon’s eleven Republican senators fled the state, preventing
the passage of HB-2020, Oregon’s carbon “cap-and-trade” bill. In spring of 2020, SB-
1530, the proposed Oregon cap-and-trade program that was modified to be more palatable
to rural Oregonians. Despite the modifications, like its predecessor, SB-1530 was again
boycotted by Republicans and defeated. Despite substantial support for a carbon tax
amongst economists (e.g., Metcalf (2009)), Oregon has been unable to pass legislation
for a carbon cap-and-trade program. Oregon’s attempts and (current) failure to create
such a program highlights the complicated and contentious political, environmental, and
social intersection concerning environmental regulation. Successful passage of a carbon
cap-and-trade in Oregon relies on understanding preferences for a number of key program
attributes.
B.1.2 Cap-and-Trade Attributes. Careful consideration was involved in
the selection of program attributes to include for the carbon cap-and-trade programs
we featured in our survey. 1 We ultimately chose to include nine total attributes for
each program, which is clearly not an exhaustive list. It is typically necessary for
choice experiments to avoid making unreasonable demands on the cognitive capacity
of respondents. So our featured attributes were selected based on their importance to
1The attributes included are: the level of carbon emission reduction, the program’s impact on carbon-
industry and green-industry jobs, the financial cost of the program to households, the program’s permit
allocation system, the use of permit auction revenue, and the program’s inclusion of additional regulations.
To see more details about our own survey instrument, see Appendix B.2 and Appendix B.3.
174
policy makers as well as the public. We will discuss briefly our motivation for including
each feature, with the exception of the emissions reduction achieved (which seems self-
explanatory).
B.1.2.1 Jobs. Perhaps the biggest political impediment for carbon cap-and-
trade programs, as for other environmental regulations, has been their potential adverse
effects on the economy—namely eliminating jobs in certain industries (Coglianese et
al. (2013)). Paramount to successful and equitable implementation of regulatory policy
is ensuring that workers and communities are protected in the transition to a greener
economy (Look, Raimi, Robertson, Higdon, and Propp (2021)). However, despite the
political clamor about job losses, there has been relatively little systematic evidence that
significant job losses accompany carbon pricing.2 Several studies have found a significant
negative impact of environmental regulation on jobs, but the authors still argue in these
cases that the benefits of the regulations (e.g. the Clean Air Act) have greatly outweighed
the costs.3 A common finding for studies that identify job losses (e.g. Yamazaki (2017);
Hafstead and Williams (2018)) is that the job losses occur in regulated sectors and are
often accompanied by new jobs in clean industries. However, it should be stressed that
it is difficult to assess substitutability among different types of jobs. Even in instances
where job losses in some sectors are offset by job gains in other sectors, there can still
be significant welfare impacts (Reed Walker (2013); ? Sovacool et al, 2021). Whether
warranted or not, concerns about displaced workers remain a key obstacle to public
acceptance of carbon emission regulations.4
2See Berman and Bui (2001), Deschênes (2012), Gray, Shadbegian, Wang, and Meral (2014), M. Liu,
Tan, and Zhang (2021), Morgenstern, Pizer, and Shih (2002), Sheriff, Ferris, and Shadbegian (2019), and
Yamazaki (2017).
3See Bartik (2013), Greenstone (2002), Reed Walker (2013)
4Some authors have questioned the validity of findings that show an impact of regulations on
employment (? Belova et al, 2015; ? Hafstead and Williams, 2019). For example, inappropriate modeling
assumptions common to most earlier research could lead to biased results (Hafstead, Williams III, and Chen
(2018); Hafstead and Williams (2018).
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B.1.2.2 Costs. Cap-and-trade programs are largely popular because of
their promise of efficiency. However, the system’s inattention to distributional impacts
have been a source of considerable concern.5. Fullerton (2011) points out that there
are a number of ways in which distributional inequities can result from cap-and-trade
programs. The most obvious is the upward pressure that cap-and-trade programs
put on prices for carbon-intensive products. If the burden of these higher prices falls
disproportionately on lower-income households, then the policy is considered regressive.
This burden could be a result of lower-income households consuming relatively more
carbon-intensive products (e.g. electric cars remain expensive) than higher-income
households. Likewise, lower-income households may spend a larger portion of their
income on carbon-intensive products (e.g. electricity bills). There is substantial evidence
that carbon-pricing policies are regressive 6. However, there is also evidence for carbon
pricing policies being progressive. 7 8 In any case, properly addressing the issue of a
regressive carbon pricing scheme is challenging because of the distributional effects vary
widely across communities and contexts 9. Conditional on the need for climate policy, it
5See (Buchs et al, 2011); Deryugina et al. (2019); Dorband, Jakob, Kalkuhl, and Steckel (2019);
Farber (2012); Feger and Radulescu (2020); Fullerton and Muehlegger (2019); ? Goudler et al, 2019[?];
W. A. Pizer and Sexton (2019); Shammin and Bullard (2009); Wang, Hubacek, Feng, Wei, and Liang
(2016); R. C. Williams, Gordon, Burtraw, Carbone, and Morgenstern (2014) Williams et al, 2015)[?]
6See Bento (2013), Buchs Barsely and Duwe, 2013; Burtraw et al. (2009); da Silva Freitas, de Santana
Ribeiro, de Souza, and Hewings (2016); C. A. Grainger and Kolstad (2010); Kolstad (2014), Jorgenson,
Goettle, Ho, Slesnick, and Wilcoxen (2013) Mathur and Morris (2014); Moz-Christofoletti and Pereda
(2021); Wier, Birr-Pedersen, Jacobsen, and Klok (2005)
7Ohlendorf, Jakob, Minx, Schröder, and Steckel (2021) point out that, even in the case of a progressive
policy, higher consumer prices still increase the risk of poverty for low-income households.
8See Beck, Rivers, Wigle, and Yonezawa (2015); Cronin, Fullerton, and Sexton (2019); Dorband et al.
(2019); and Devarajan (2013).
9(See Rausch, Metcalf, and Reilly (2011); Ohlendorf et al. (2021); Fullerton, Heutel, and Metcalf
(2012); Pashardes, Pashourtidou, and Zachariadis (2014); Fischer and Pizer (2019); Dorband et al. (2019);
W. Pizer, Sanchirico, and Batz (2010); Jorgenson et al. (2013); W. A. Pizer and Sexton (2019); and Burtraw
et al. (2009)
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is possible that market mechanisms, while regressive, could be less regressive than other
approaches to carbon management (e.g., see Borenstein and Davis (2016)).
B.1.2.3 Permit Allocation. Permit allocation has proven itself to be one of
the key design features cap-and-trade programs.10 Emission permits are allocated either
based on historical output, through a government-coordinate auction, or a combination of
the two Fischer and Fox (2007) [?](Fischer and Fox, 2007). The benefit of basing permit
allocation on historical output is primary attributed to improving political feasibility and
reducing the economic burden on firms. However, there is considerable criticism of this
allocation system. ([?][Huber 2013], Vesterdal and Svendsen (2004) and Mackenzie,
Hanley, and Kornienko (2008)). While politically less-palatable, permit auctioning is
argued to be the welfare improving option (Cramton and Kerr (2002), Betz, Seifert,
Cramton, and Kerr (2010), [?] [Belifiori, 2017], and Farber (2012).)
B.1.2.4 Permit auction revenue use. A decision for the government to
auction emission permits will lead to a new source of revenue for the government. This
revenue could be recycled to ameliorate the distributional issues. 11 Three particular
uses are modeled in this study: subsidizing emission-reducing equipment for firms
and households, financing adversely affected workers and communities transition, and
reducing state taxes. Research has found that revenue recycling and providing the public
with tangible public benefits could significantly improve support for carbon pricing
(Amdur et al. (2014); Beiser-McGrath and Bernauer (2019); Raymond (2019)). One
10Price collars and permit banking are also important considerations of the permit system (Fell, Burtraw,
Morgenstern, and Palmer (2012), Fuss et al. (2018), Metcalf (2009), Murray, Newell, and Pizer (2009),
Hasegawa and Salant (2015), Burtraw, Evans, Krupnick, Palmer, and Toth (2005), and Metcalf (2009)
11See Boyce (2018); [??] Buchs Barsely and Duwe, 2013; [??] Metcalf 2008; Dinan and Rogers (2002);
Wang et al. (2016); Bento (2013); Goulder et al. (2019); Farber (2012); [??]Williams et al 2015; Parry and
Williams (2013); Feger and Radulescu (2020); C. A. Grainger and Kolstad (2010); Moz-Christofoletti and
Pereda (2021); Aubert and Chiroleu-Assouline (2019); W. A. Pizer and Sexton (2019).
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caveat to this work is noted by ?? Sallee (2019), who argues that using revenue recycling
cannot achieve a Pareto improvement.
B.1.2.5 Additional Regulations. Climate Change’s impacts epitomize
the issues of the environmental justice movement.12 However, despite being one
type of a climate change mitigation policy, carbon cap-and-trade programs also raise
environmental justice concerns (Farber (2012), Fowlie et al. (2020), Kaswan (2008)). The
primary concern is that a market-based system will inevitably lead to a disproportionate
accumulation pollution (i.e., “hotspots”) in marginalized communities, while the benefits
of the program are enjoyed by higher-income and more-empowered communities (Fowlie
and Muller (2019). Research has turned up little evidence to substantiate this concern
(C. M. Anderson et al. (2018), Corburn (2001), Farber (2012), Fowlie et al. (2012), and
Fowlie et al. (2020). Hernandez-Cortes and Meng (2020) used a dispersion model and
find that, under California’s carbon cap-and-trade program, environmental equity has
actually improved.13 One hypothesis is that the dirtiest places are also the cheapest to
clean up (Currie, Voorheis, and Walker (2020)). On the other hand, C. Grainger and
Ruangmas (2018), contrary to Hernandez-Cortes and Meng (2020), use a dispersion
model to demonstrate that low-income communities have been exposed to more pollution.
[??] Chan and Morrow (2019) find, however, that under the Regional Greenhouse Gas
Initiative in the northeastern United States, electricity generation has shifted relatively
towards areas with higher marginal damages from SO2 emissions. Some argue that
carbon cap-and-trade programs are not the tool to address other pollutants and should
only be relied upon only to address carbon emissions (e.g., Fowlie et al. (2020); Dulaney,
Greenbaum, Hunt, and Manya (2017)). Like other distributional issues, others contend
12Mohai, Pellow, and Roberts (2009) give an excellent overview of Environmental Justice and Banzhaf,
Ma, and Timmins (2019) provide another good overview more specifically prepared for economists.
13Shapiro and Walker (2021) similarly find that offsets do not seem to have created hotspots in California
in relation to race or class.
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that despite their challenges, properly designed cap-and-trade programs can mitigate most
threats that these programs pose to environmental justice (e.g. Farber (2012); Kaswan
(2008).
B.1.3 Political Obstacles. Notwithstanding the considerable economic
challenges of designing an optimal carbon cap-and-trade program, perhaps the biggest
impediment to policy adoption in the United States is political obstacles (Goulder and
Parry (2008); Berrens et al. (2004); Klenert et al. (2018). And at the end of the day, a
policy’s economic implications are irrelevant if the policy is not passed by lawmakers.
Indeed, economic analysis of environmental regulations frequently has little bearing
on political popularity (Gillingham et al. (2018)). In part, this is due to compromised
government integrity (Baranzini and Carattini (2017); Convery and Redmond (2013)).
However, the primary reason carbon cap-and-trade programs and other carbon pricing
policies remain largely politically infeasible is due to the public’s lack of support (Levi,
Flachsland, and Jakob (2020)).
Public support for a policy is highly dependent on the narrative surrounding the
policy, as well as the framing of the policy (Alló and Loureiro (2014); Carattini et al.
(2018); Bilandzic, Kalch, and Soentgen (2017), Bushell, Buisson, Workman, and Colley
(2017); Dickinson, Crain, Yalowitz, and Cherry (2013); Terzi (2020)). A considerable
amount of effort on the part of energy-intensive corporations has gone toward fostering
opposition to climate-change-related policies through misinformation campaigns (Egan
and Mullin (2017), Farrell (2016), Westervelt (2018)). Additionally, conservative
regulation-opposing politicians have used public concerns about the economy to establish
an anti-environmental regulation narrative (Coglianese et al. (2013); Egan and Mullin
(2017)). The effects of these campaigns can be seen in research which reveals that the
more people understand the impacts of climate change, the more they are willing to
participate in (or bear the costs of) climate-change mitigation measures (Bord, O’Connor,
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and Fisher (2000); Videras, Owen, Conover, and Wu (2012), Spence et al. (2011),
Scannell and Gifford (2013), and Bain et al. (2012)).
In the United States, political party affiliation is often the primary determinant
in attitudes about climate change and mitigation policies. A review of climate change
opinion surveys in the United States finds that not only is partisanship the paramount
driver in support for policy, but that the gap between the Republicans and Democrats
has become even more pronounced in recent years (Egan and Mullin (2017)). This
assessment has been corroborated using revealed preference studies as well. For example,
S. Anderson et al. (2019) use voting data from two failed carbon tax bills in Washington
State and find that political party affiliation is by far the biggest indicator of support
or opposition to the policies. In their study, political ideology accounts for 91% of the
variation in vote shares across precincts.
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B.2 Appendix: Structure of the Survey
B.2.1 Demographic Questions for Screening. The first section of the
survey collects five basic pieces of information about the respondent: place of residence
(state), age, gender, race, and income. A sixth question asks the respondent to report
their Oregon zip code. Their response is cross-referenced against an exhaustive list of
Oregon’s residential zip codes. What we call “Demographic Questions for Screening,”
serves multiple essential purposes.
First, in order to measure heterogeneous willingness to pay (WTP) measures
across demographics it is essential that we in fact know what are those demographics.
Second, we would like our 1000 observations to be as representative of Oregon, at
least on those five categories, as possible. If the respondent answers the six questions
(e.g. White male, age 25-34, with income $20,000 - $24,999 a year, and lives in the
zip code 97219) and we observe that we already have “enough” respondents fitting that
description, then we excuse the respondent from the rest of the survey.
Finally, the preliminary demographic section allows for sample selection
correction. Before any information alluding to the content of the survey is revealed (i.e.
that the survey is asking about WTP for a carbon cap-and-trade program), the respondent
must answer those five basic questions. If the respondent chooses “Prefer not to say” for
any of the categories then they are excused from the survey. If the respondent answers the
demographic questions and we deem them eligible for the survey (see the second point
above) then we introduce the topic of the survey. At this point, some respondents will
drop out of the survey. However, because we have already gathered the demographic
information about these dropouts we are able to observe what relationship, if any,
exists between willingness to take the survey and the aforementioned demographic
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characteristics. In other words, we are able to observe if sample selection is occurring
and correct for it.14
B.2.2 Intro Questions. After completing the initial demographic
information, the respondent is sent to the “Basic Information and Consent” page. It is
at this point that the topic of the survey is revealed. The respondent is asked to consent
to taking the survey. A followup question asks the respondent to confirm that they will
provide “thoughtful and honest answers” as recommended by Johnston et al (2017). A
“No” to either of these questions results in termination of the survey.
B.2.3 Background Information. The next section of the survey provides
the respondents with some basic information that is relevant to carbon cap-and-trade
(CAT) programs. We begin with a brief explanation of climate change, carbon emissions,
and the relationship between the two. We then explain the motivation of understanding
Oregonians’ preferences concerning a CAT program. Namely, that Oregon legislators
have attempted to pass a CAT in Oregon but have failed to do so in large part because
specifics of the program were not agreeable. At this point we briefly explain the
mechanics of a CAT. The respondent is then prompted with “How familiar are you with
carbon cap and trade programs?” The respondent receives more information about how a
CAT works if they answer “I should probably review the basics” or “Not familiar at all.”
The respondent skips this further explanation if they answer “Quite familiar.” After the
explaining the broad strokes of CAT programs, the survey elucidates which companies
will likely be targeted in Oregon. While we cannot know what form policy will take
in reality, it is important that the respondents have a similar idea of who is regulated
while answering the survey. Because the hypothetical CAT programs our survey asks
respondents to make choices about include specific rules about permits15 we provide a
14See Appendix B.4 for explanation of the selection correction procedure.
15See Choice Scenarios below.
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cursory explanation of permits that complements the earlier explanation of carbon cap-
and-trade programs. The respondents are able to pursue a more detailed explanation
of permits if they feel inclined. The more detailed explanation does not include unique
information, but rather provides a fuller explanation that might be more accessible should
the cursory explanation leave respondents confused. The next two pages of the survey
describe respectively penitential benefits (global and local) and costs (to households, to
businesses, and concerns about equity). The final page of this section asks the respondent
which county they live in. Using that response we are able to scale the values of the
choice tasks to the county level the individual respondent lives in.
B.2.4 Tutorial on Program Attributes. The next section of the survey’s
purpose is to prepare respondents for the choice tasks. Each choice task presents a
hypothetical program in the form of a table. Due to the complexity of the table it is
appropriate to send some time explaining all the moving pieces of the choice task.16
The table is codified into five “Feature Groups”: Results, Carbon Permits, rules, Auction
Revenue Uses, Additional Regulations, and Cost to your household. Each group has
between 1 and 3 different features for a total of nine program features for respondents to
consider. The nine program features are discussed below. The tutorial walks respondents
through each feature of the table. A brief explanation of the feature is provided as well
as a graphic that helps explain and provides relief from too much text. In addition to
the explanation in the tutorial, the respondents are instructed that throughout the choice
tasks a abbreviated description of any specific feature can be called up by clicking on that
feature in the table. The values used in the tutorial section are the same values used in the
first choice task. This is done to minimize mental effort on the respondent’s behalf and
to help connect the tutorial with the choice task section. Before the feature-by-feature
16Pretesting found that thorough explanation was often necessary to convey the parameters of the
hypothetical situation we were asking respondents to consider.
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portion of the tutorial begins, respondents are instructed that the every program displayed
in the choice task will begin January 1, 2023. Consequently, the various effects of the
program will also begin to accrue January 1, 2023.
Results
The first feature group, Results, has three attributes: Carbon emission reduction,
Carbon industry jobs lost, and Green industry jobs gained. The first feature, carbon
emission reduction, refers to the percent reduction of total annual carbon emissions
in Oregon by the year 2050 (relative to current emission levels). By clicking on a link,
respondents are able to observe current emission levels in Oregon, which provides context
to the reduction goal.
The next feature is carbon industry jobs lost. The value presented in the table is
not a percent of jobs lost, but rather a sum (e.g. 2,000 jobs). This sum is based in part
on the county that the respondent indicated they lived in earlier in the survey.17 The
respondents are instructed that they should imagine this job loss would occur over the
next 30 years–consistent with the carbon emission reduction by 2050. Respondents are
able to see how many current18 carbon industry jobs are in the respondent’s own county
of residence. Respondents are also shown the total number of carbon industry jobs in
Oregon.A link is included that clarifies what the survey means by “carbon industries.”
Green industry jobs gained follows the same format as carbon industry jobs lost
with the obvious exception that values are based off of green industry jobs, as defined by
the BLS.
Carbon Permits, rules
17We take the current level of carbon industry jobs in a county (e.g. 40,000) and then scale that number
by a randomly generated percent (e.g. 5%) and present that number (e.g. 2000) as the number of carbon
industry jobs lost.
18Calculations use data from 2019 for the Bureau of Labor Statistics
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Carbon Permits, rules has only one feature: Share of permits auctioned. This
value indicates the percent of the total cap set by the cap-and-trade program that is
auctioned. The respondent is reminded that the rest of the permits are allocated for
free. The survey does not specify the allocation process, but examples are provided
for respondents who are curious earlier in the survey. Respondents have already been
provided with information about permits earlier in the survey, but it is important that
respondents clearly understand the costs and benefits of this feature. In the pretest,
initially testers were often unclear about how this feature worked. The survey includes
a detailed visualization of the permit rule system to aid in the explanation.
Auction Revenue Uses
The next feature group is Auction revenue uses. One of the primary issues to
political feasibility of cap-and-trade programs is concern over some groups (e.g. coal
miners or low-income households) being economically devastated by shrinking industries
or higher costs of goods. A popular, in theory, way to address this heterogeneous burden
is by using the funds from the auctioned permits to target groups or sectors in need of
assistance. After consideration, this survey asks respondents to consider three possible
ways to spend the auction funds: fund new equipment, support communities/workers,
and Oregon tax relief. There are a multitude of other ways this money could be spent,
but we found these categories to be a good balance of both encompassing most of the
ways as well as specific enough for respondents to be able to consider clearly. The values
presented are in percent terms (summing to %100 across the three uses). Because no
specific dollar value is given in terms of total money raised by the auction, respondents
similarly do not see a specific amount of money being allocated to these three uses.
Fund new equipment refers to revenue spent to partially or entirely subsidize the
purchase of emission reducing equipment for firms or households. In practice, the more
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general label for spending of this nature might be referred to as “funding green projects.”
However, that label is fairly vague and we believe that being more specific would result in
more thoughtful responses.
Support communities/workers refers to revenue spent on communities or workers
in certain industries that bear a relatively heavier burden of the costs of the cap-and-trade
program. Often referred to as a Just Transition, an essential component of a politically
feasible program includes a safety plan for those hurt by the program. Some examples
are given, for instance “communities with a lot of carbon-intensive jobs.” However, no
specific group is explicitly stated as receiving these funds. Furthermore, the vehicle in
which the funds are delivered are also left open-ended.
Oregon tax relief refers to revenue spent on reducing the Oregon state taxes. A
considerable amount of literature explores the various intricacies using taxes to counteract
the costs of carbon pricing. However, in the survey we keep the idea simple to reduce
mental effort on the behalf of the respondent. In short, the higher the value this feature
takes on the lower “taxes” will be for Oregonians.
Additional Regulations
Additional Regulations has only one feature limit other pollutants. This feature
is included ad hoc to address environmental justice concerns about unintended hot spots
of carbon emission co-pollutants. Under a standard cap-and-trade program, it is possible
that certain firms will actually increase emissions and thus increase co-pollutants (e.g.
NOx or PM2.5). The limit other pollutants feature takes on two values, “YES” and “NO.”
Respondents are instructed of the potential issue of unintended co-pollutant hot spots
under a carbon cap-and-trade program and then this feature indicates whether some form
of “additional regulation” would be part of the program. The details of the regulation
are left vague, and in practice there are many ways to address the co-pollutant issue (e.g.
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pollution standard, trading ratio or zonal trading). However, we believe this approach to
be a good compromise of an accessible idea for respondents that addresses a key issue in
carbon cap-and-trade programs.
Cost to your household
The final feature of the table is the cost to households in Dollars per month.
Dollars per month is explained as the “average monthly costs your household would bear
if the program is adopted.” We use the per month unit of time because energy bills, as
well as consumption budgets, are frequently considered on a monthly scale. For many
households these will be the primary sources of program costs. The respondents are
instructed that these costs are unavoidable. A change in energy use or not working in a
carbon-intensive industry does not absolve the respondent’s household from incurring the
cost.
B.2.5 Choice Scenarios. Each respondent is asked to perform six choice
tasks (Program A through Program F). In each choice task they are presented with a
hypothetical program in the form of a table (with the features mentioned above) and
asked if they would prefer the program or no program. Each program is identical in
display and content with the exception of the values that each feature takes on. To reduce
mental effort on behalf of the respondent, Program A uses the values displayed in the
program attribute tutorial. The choice is presented as a “vote.” The idea being, it is
quite conceivable that a cap-and-trade program could be on a future ballot in Oregon
so the survey does its best to replicate that scenario. This is one way in which the survey
addresses the cheap talk issue that is common in contingent valuation methodology.
In a preamble to the first program (Program A) the respondents receive a few
additional instructions. First, they are told that the labels of the programs (A through F)
are arbitrary and have no relation to the quality of the program. The preamble also clearly
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states that in for any given program the respondent should only consider this program
and no program at all. In other words, we do not want respondents voting against, for
instance Program C, because they prefer Program B or some other program that they
have conjured up in their head. This point is belabored by making the voting choices
for each program “Program X to begin January 1, 2023” and “No program at all.” The
respondents are instructed that voting against a program is a valid choice and that they
should act freely since the researchers will not learn their identity. In an additional effort
to address cheap talk respondents are instructed that, “In hypothetical choices such as
these, people sometimes do not think carefully enough about what they would have to
give up to be able to pay the monthly cost of the program. Please consider what your
household would have to sacrifice, if the proposed cap-and-trade program were
adopted.”. Finally, respondents are reminded that they are able to review explanations
for a program feature by clicking on it in the table.
The survey is designed such that the entire program table is visible on a screen–
this includes cell-phone screens. We presume that many respondents will use cell-phones
to take the survey and in order to consider all the features of a program the respondent
should be able to see them all at the same time. Below each program table the respondent
is prompted with, “If Program X were the only program to be put to a vote, I would vote
for:” followed by the two aforementioned choices.
After the respondent votes on Program A they are taken to different pages
depending on their choice. If the respondent votes for Program A they are sent to the
next choice task. If the respondent votes for no program they are asked to indicate from a
menu of options all the reasons they voted against the program:
– Too much emission reduction
– Too little emission reduction
– The economic impacts were too costly
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– Did not approve of the auction revenue use
– Too many permits were auctioned
– Too few permits were auctioned
– Did not approve of the Additional Regulations on other pollutants
– The benefits of Oregon or the World do not justify ANY cost
– Program A did not seem believable
– Some other reason
We are able to deduce from the respondents choices here whether they have valid
economic reasons for voting no, or whether their no vote signals scenario rejection. 19
From this page, people who voted no on Program A are then asked if they would
vote for any carbon cap-and-trade program. More specifically they are asked to choose
from three options: “I did not like Program A, but there might be some type of program,
at some cost low enough for me, for which I could possibly vote ’Yes”’, “Carbon cap-
and-trade programs are a BAD idea. The government should not interfere with the free
market. I would vote “No” for ANY carbon cap-and-trade program!” and “Something
needs to be done about carbon emissions, but a carbon cap-and-trade program is not
the solution.” If the respondent indicates that there is a program they could conceivably
vote for they are sent to the Program B choice task. If at this point the respondent
indicates they would not vote for any carbon cap-and-trade program they are skipped
through the choice tasks to the next section of the survey–this saves the respondent
unnecessary effort. If the respondent indicates that something needs to be done about
carbon emissions, but the solution is not cap-and-trade they are sent to a further clarifying
page.
19An example of a valid reason would be “The economic impacts were too costly.” An example of an
invalid reason would be “Too little emission reduction.” We consider this an invalid reason, because the
alternative to Program A is no emission reduction. So this answer indicates that the respondent is not
operating in the framework of the hypothetical scenario.
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If a respondent votes against Program A and indicates that carbon cap-and-trade
programs are not the appropriate policy response they are asked if they would prefer a
carbon cap-and-trade program to no policy at all. If at this point they indicate that they
would prefer a cap-and-trade program to nothing at all they are sent to the Program B
choice task. If they are staunchly opposed to cap-and-trade programs they are skipped
through the choice tasks. Respondents who end up at this page are asked what policy they
would prefer to a cap-and-trade program. This is asked after completing the choices tasks
or after being skipped through the choice tasks as determined by their answers.
After completing the choice tasks, respondents are asked to indicate which of the
program features were most important to them. For respondents who made it through all
choice tasks but voted for no in all six choice tasks, they are asked to explain the reasons
they did so. They choose from a menu of options:
– I am not convinced that climate change is actually happening
– Even if climate change is actually happening, I don’t believe that anything we do
(or don’t do) will make any real difference
– I don’t think Oregon produces enough carbon emissions to matter. Instead, states
and countries with more heavy industries should be required to cut back
– I would be hurt by the effect of the program on my livelihood or the cost of things I
buy
– I would be hurt by the effect of the program on the cost of transportation
– These choice tasks were just too difficult for me to process
– Some other reason (Please specify)
In this way we are able to gain a better understanding of what features are important to
them, despite having no “choices.”
B.2.6 Follow-up Questions. In the final section of the survey the respondent
is asked a serious of additional socio-demographic questions. Some of these questions
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would be quite informative if asked to ask in initial demographic question section. For
instance, political ideology and political party affiliation are likely determinants in a
respondent’s propensity to dropout of the survey. However, due to IRB restrictions this
is not possible.
Years in Oregon
Two questions are asked concerning respondents’ residence in Oregon. First we
ask respondents “How many years have you lived in Oregon” (with a sliding scale from
0 - 100), and then we follow up with “How many more years do you expect to keep living
in Oregon?” (with a sliding scale from 0 - 100). These questions are included for two
separate purposes. The first is to test the hypothesis: Are people who feel more connected
to a geographic area (in this case, Oregon) more likely to support long term environmental
policy (in this case, carbon cap-and-trade) in that area? The second purpose of this
particular pair of questions is to screen out inattentive/careless respondents and bots.
Both can potentially be detected by illogical uses of the sliders–especially when cross-
referenced against the age question asked at the beginning of the survey. For instance,
bots are often programmed to max out sliders. In this case answering 100 years to both
years lived so far and future years lived in Oregon will raise a flag.20
General Socio-demographic Questions
We include a series of additional basic socio-demographic questions. The
questions are multiple/single choice, with the inclusion of “Prefer not to say” for each
question, unless stated otherwise. We force a response to the questions but a respondent’s
20A very detailed assessment of invalid responses in an online survey panel was provided by Robert
Johnston in a session entitled “Contemporary Guidance for Stated Preference Studies: An Update
(roundtable)” at the 2021 Annual Conference of the Society for Benefit-Cost Analysis.
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choice of “Prefer not to say” does not end the survey for them at this point. The questions
in the order that they appear are:
– What is your ethnicity?. Choices include: “Hispanic,” “Non-Hispanic,” or “Other.”
– Which industries provide a significant amount of your household’s income?. We
provide a menu of standard NAICS categories with specifically relevant subsectors
broken out separately (e.g. Wood Product Manufacturing and Forestry/Logging are
separate categories).
– Politically, do you consider yourself to be:. Choices range from “Strongly
conservative” to “Strongly liberal.”
– What political party do you most strongly identify with?. Choices include:
“Republican,” “Democrat,” and “Independent.”
– What is your highest level of education?. Choices include: “Less than high school,”
“High school graduate,” “Some college,” “Bachelor’s degree,” “Master’s degree,”
“Doctoral degree,” and “Trade or technical school.”
– Which best describes your current employment status?. Choices include: “Self-
employed or small business owner,” “Employee, working full-time,” “Employee,
working part-time,” “Not employed, looking for work,” “Not employed, NOT
looking for work,” “Retired,” “Disabled, not able to work,” “Full-time student,”
“Student with part-time work,” and “Other.”
Attitudes about Climate Change
Respondents are asked a serious of questions pertaining to their attitudes about
climate change. Recall that in the background information section of the survey climate
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change was briefly discussed. The survey takes the stance that climate change is real,
which can be, unfortunately, read as a political stance by some Americans. It is likely that
people willing to participate in the survey will need to have some basic acceptance that
climate change is real. However, it is informative to have a more nuanced understanding
of respondents’ attitudes.
Respondents are prompted with, Climate change is real, and is a serious threat to
humanity. Response options include: “Strongly agree,” “Agree,” “Neutral,” “Disagree,”
and “Strongly Disagree.” If the respondent selects “Strongly disagree” they are skipped
past the remainder of the climate change questions.
If they choose any other option respondents are prompted with, Climate change
is the result of human activity. Response options include: “Strongly agree,” “Agree,”
“Neutral,” “Disagree,” and “Strongly Disagree.” If the respondent selects “Strongly
disagree” or “Disagree” they are skipped past the remainder of the climate change
questions.
Finally, respondents are asked, Who is most responsible for slowing or preventing
climate change? (Select all that apply).Response options include: “Local governments,”
“The Federal government,” “Households,” “Companies,” “People who are wealthier,”
“People who are responsible for more emissions,” “Other” and “Everyone equally.”
Generational Questions
Following the climate change attitude portion of the survey, respondents are then
asked two generational questions. First they are asked, Do you have any of the following?
(Check all that apply) with response options of: “Children,” “Grandchildren,” “Great-
grandchildren,” “Other descendants (please specify),” “None of the above,” and “Don’t
know / not sure.” They are then asked, How many generations back can you trace at least
some of your ancestors? (Check the greatest number) with response options ranging from
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“1 generation (i.e. just your parent(s))” to “7 or more generations.” The hypothesis is that
people who see themselves as being remembered as well as they remember their ancestors
might be more concerned about climate change and what they do about it now. While the
questions perhaps appear non sequitur, being too direct in testing this hypothesis would
potentially lead to social desirability bias.21
Energy Use Questions
Respondent’s are asked two questions concerning fuel-type. First respondents
are asked, What is the primary fuel you use to heat your dwelling?. Response options
include: “Natural gas,” “Electricity from a conventional power plant,” “Electricity from
solar panels or wind power,” “Electricity (unsure about source),” “Wood or wood pellets,”
“Passive solar (heated water),” “Other (please specify),” “I don’t heat my dwelling,” and
“Don’t know / not sure.” Respondents are also asked to indicate What are your most
common forms of transportation? (Check as many as apply). Response options include:
“Personal vehicle (gasoline or diesel),” “Personal vehicle (hybrid),” “Personal vehicle
(electric),” “Public transportation (bus or train),” “Taxi or ride-sharing (e.g., Uber or
Lyft),” “Bicycle,” “Walking,” and “Other (please specify).”
It is likely that a large portion of the average costs to households resulting from a
carbon cap-and-trade program will come through the form of higher energy prices. While
we have already managed to glean information about respondents’ attitudes concerning
higher energy costs it is informative to be able to connect a respondent’s attitude about
higher costs and their actual energy use. While in the choice task we instruct respondents
to assume costs are unavoidable, it is likely that higher energy costs would be more
salient for those that use natural gas to heat their homes or always commute via a personal
21Respondents answer how they would like to be seen rather than how they actually feel. While an online
survey format helps mitigate this, a loaded question like, “Do you care about future generations?” could
lead to untruthful responses.
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vehicle.22 Energy-type use also helps identify which individuals are willing (and able)
to make personal efforts to mitigate climate change. Identifying this preference is
informative in our WTP analysis.
Feedback Questions
We give respondents three separate prompts to provide feedback on the survey.
The feedback, in addition to informing future studies, also aids in our data collection.
The first feedback prompt is concerned with research team bias. There are two
versions (version A and version B) of the prompt page that are randomly assigned to
individual respondents. Both version A and B of the prompt page read, It seemed like
the research team wanted me to:. The difference in the versions is that the order in
which the menu of response choices is inverted fro version B. The response choices, in
the order that they appear in version A, include: “definitely vote AGAINST a carbon
cap-and-trade program,” “probably vote AGAINST a carbon cap-and-trade program,”
“vote according to my own beliefs,” “probably vote FOR a carbon cap-and-trade
program,” and “definitely vote FOR a carbon cap-and-trade program.” To reiterate,
version B has the same choices but an inverted order. The randomized inversion of the
response choices is to test for response order bias from the respondents. An ideal survey
would result in all respondents choosing “vote according to my own beliefs.” However,
non-systematic even distributions “probably vote AGAINST a carbon cap-and-trade
program,” “vote according to my own beliefs,” and “probably vote FOR a carbon cap-
and-trade program” are also acceptable. It is possible that due to the politically charged
nature of climate change and related policies, that simply asking about attitudes toward
22It should also be noted that higher energy costs are also more salient for low-income households,
because a larger portion of their income goes towards energy use. Recall, income level is one of the
demographic pieces of information that is required in order to be eligible for the survey.
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a carbon cap=and-trade program will lead the respondent to assume the research team is
biased in favor of a program.
The second feedback prompt asks the respondent to rate the survey using a five
star rating system on four categories: “Understandable,” “Relevant to you,” “Interesting,”
and “Informative.” In addition to providing useful feedback to future studies, this prompt
also serves two additional purposes. First, low scores, especially for “Understandable,”
give us an idea about the quality of a particular respondent’s submission. If a respondent
only gives the survey 1 out of 5 stars for “Understandable” then we know that the choice
tasks were likely not performed with full comprehension. Second, this star system
provides another chance to draw attention to respondents (or bots) who are speeding
through the surveys.
Finally, respondents are given an open-ended prompt for feedback. The primary
goal of this prompt is to detect respondents who are speeding through the survey or bots.
Bots in particular will often enter gibberish or nonsensical answers. Of course, it always
encouraging to read thoughtful comments from respondents.
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B.3 Appendix: One Instance of the Survey (Screenshots)
B.3.1 State of residence. The screening questions on the first 8 pages of
this survey of Qualtrics panelists are completed before the page that contains the Consent
to Participate in the actual survey. The Consent page is where the respondent first learns
about the topic of the survey. This ordering is crucial to any ability to model systematic
response/non-response (attrition from the random sample of Qualtrics panelists).
Qualtrics prefers that respondents who are ineligible because quotas have already been
met should be apprised of this fact before they get too far into a survey for which their
answers are not needed. We require that potential respondents, still naïve about the topic
of the survey, should at least be willing to supply their state of residence (always Oregon
for this study) their age, gender, race, and household income bracket. These are the quota
criteria for inclusion.
However, we also require that they enter their ZIP code at the end of the screening
section. Our overall target sample (1000) is not large enough to warrant quotas by ZIP
code within Oregon, but we need this information to permit us to link every one of these
screened and eligible respondents to external auxiliary data that can be geocoded to
ZIP codes. For this climate-related study, these external data sources include Census
ZCTA data, NOAA climate division data, 2020 Presidential election data by county,
state legislative district voting data for Oregon for 2016, along with spatial data on the
recent history of wildfires and drought levels. These neighborhood/county characteristics
can be used as proxies for the salience of climate change problems to people who live
in the same area as the eligible respondent. The partisan reactions to Oregon’s actual
proposed carbon cap-and-trade programs in recent years suggests that political ideologies
in the respondent’s neighborhood may make programs to reduce carbon emissions either
very attractive or readily dismissed. For the latter group, we expect a lower likelihood of
continuing with the survey to completion, after the topic of the survey is revealed.
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Qualtrics can target Oregon in issuing survey invitations. However, to prevent
non-Oregonians from pretending to be from Oregon, we first check to see whether
respondents choose "Oregon" when given an opportunity to choose their state. (If they
don’t choose Oregon, they are given one opportunity to choose again, and are terminated
if they don’t choose "Oregon" at least on the second try. The follow-up double-check
page is not shown here.)
B.3.2 Age.
B.3.3 Gender.
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B.3.4 Race.
B.3.5 Household income.
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B.3.6 ZIP code. We validate the respondent’s zip code entry by checking
it against a list of “standard” Oregon ZIP codes—namely ZIP codes that are not for
post-office boxes and are not “unique” (typically for government agencies or other large
institutions that have their own internal mail systems). Unique ZIP codes are more likely
to be workplaces.
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B.3.7 Check ZIP code.
B.3.8 Confirm standard ZIP code.
B.3.9 Consent to Participate. This page is where respondents first learn
the topic of the survey. We expect that upon learning that the survey will be about carbon
cap-and-trade programs to deal with climate change, some share of respondents to lose
interest, while others will find the topic especially salient. The questions asked prior to
this page allow us to assemble ZIP-code-level, county-level or other geo-coded variables
that can help us identify the respondent’s community and how its characteristics may be
systematically different than the neighborhoods of other potential respondents who either
do, or do not, continue to complete the entire survey.
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B.3.10 Oath.
B.3.11 Introduction to climate change.
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B.3.12 Introduction to carbon emissions.
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B.3.13 Introduction to controversy of cap-and-trade in Oregon.
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B.3.14 Introduction to cap-and-trade programs.
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B.3.15 Introduction to program coverage.
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B.3.16 Introduction to program coverage, continued.
B.3.17 Introduction to permit auctions.
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B.3.18 Introduction to grandfathering process.
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B.3.19 Introduction to revenue distribution.
B.3.20 Introduction to benefits of carbon emissions reductions.
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B.3.21 Introduction to possible distributional concerns.
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B.3.22 Oregon county of residence. The respondent selects an Oregon
county from the drop-down list provided.
B.3.23 Confirm county of residence. If this confirmation page shows that
the respondent checked the wrong county, they get to choose again, after which we just
have to assume that they have the right county. This page runs some javascript in the
background to associate a variety of county variables with the respondent’s own county,
and these variables are quoted later in the survey as the effects of each proposed cap-and-
trade program are described in quantitative terms.
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B.3.24 Introduce program summary tables.
B.3.25 Explain Feature Group 1.
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B.3.26 Explain Feature Group 2.
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B.3.27 Explain Feature Group 3.
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B.3.28 Explain Feature Group 4.
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B.3.29 Explain Feature Group 5.
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B.3.30 Program A choice.
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B.3.31 Follow-up to “No” vote: Reasons for vote.
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B.3.32 Follow-up to “No” vote: Will you always vote no?.
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B.3.33 Program B choice.
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B.3.34 Program C choice.
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B.3.35 Program D choice.
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B.3.36 Program E choice.
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B.3.37 Program F choice.
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B.3.38 Follow-up to “No” vote. For any of Program A through Program
F, if the respondent votes “No” on that program, the survey follows up with the list
shown on this page, of potential reasons for voting against these programs. We opted
to show this follow-up question only in association with Program F, to avoid repeating the
identical screenshot every time.
B.3.39 Preferences for policies other than cap-and-trade.
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B.3.40 Most important attributes.
B.3.41 Attachment to Oregon.
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B.3.42 Ethnicity.
B.3.43 Sectors providing household income.
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B.3.44 Political ideology.
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B.3.45 Political party identification.
B.3.46 Educational Attainment.
B.3.47 Employment status.
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B.3.48 Attitude: climate change real and serious.
B.3.49 Attitude: climate change human-caused.
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B.3.50 Attitude: responsibility to fix climate.
B.3.51 Inter-generational concern: descendants.
B.3.52 Inter-generational concern: ancestors.
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B.3.53 Primary heating fuel used.
B.3.54 Usual forms of transportation.
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B.3.55 Perception of researcher bias. This question about research bias
was randomly presented in one of two orders for the answers. Half of respondents saw
a list that put “definitely vote FOR a carbon cap-and-trad program” at the top. The other
half saw the same list, but in reverse order. This is intended to minimize any systematic
order effects if the order is not included as an explanatory variable.
B.3.56 Attitude: Respondent’s experience with survey.
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B.3.57 Feedback text message.
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B.4 Appendix: Selection Model and Selection Correction
For this paper, we correct for sample selection in terms of the willingness of
individuals to complete a carbon cap-and-trade survey. However, another potential type
of sample selection remains unavoidable: people who are willing to take an (internet)
survey upon an invitation from Qualtrics may not be representative of the general
population. While this other form of sample selection is perhaps of lesser concern, it
exists nonetheless for every consumer research panel and is difficult to address.
B.4.1 Variable Selection.
B.4.1.1 Inventory of candidate explanatory variables. To correct for sample
selection, we use a probit model to estimate an invited participants propensity to complete
the survey. We have relatively little information for every invited participant beyond their
age, sex, race and income, but we also elicited the ZIP code where they live (prior to these
potential respondents learning the topic of our survey). Thus, for a large share of these
invited participants, we can merge in ZIP-code-level neighborhood characteristics as
potential determinants of their interest in participating in a survey about climate policy.
When creating the zip-code-level profiles, we cast a wide net to find candidate
explanatory variables. The external data sets we employed to create profiles of each
respondent’s neighborhood include: the American Community Survey 5-year ZCTA-level
data (2014-2019), the MIT Election Data and Science Lab’s County Presidential Election
Returns (2020), Oregon State Office Returns for 2016 state legislative district votes
(by major party), drought data from National Drought Mitigation Center, and wildfire
data from Wildland Fire Decision Support System. We create population proportion
sociodemographics (e.g. share of the population for each ZIP code that has access to
the internet) as well as a number of climate-related statistics for each zip code (e.g.
Drought Monitor rating, or distance to the nearest wildfire in 2020). The zip-code-level
profiles are constructed to capture political ideologies, salience of climate change, and
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other sociodemographics that we hypothesize may impact each potential respondent’s
propensity to continue with the survey, to completion, after learning its topic.
It is not feasible to include, simultaneously, the full set of variables (self-reported
screening sociodemographic variables from the survey and all the available zip code
variables, and their interactions) in a single probit model. This is far too large a list
of variables, given that we have only 1630 invited participants and 1050 completed
survey questionnaires. Thus we resort to LASSO methods, in R, to pair down the list
of potentially useful explanatory variables. We use all of our available data from panelist
profiles (gender, age, race, and income bracket) as well as all our assembled geo-coded
data linked to each invited participant by their zip code (where zip code is available), as
potential regressors for our selection model.23
If a respondent drops out of the survey at any point after the consent page, they
are considered non-respondents and get the value of 0 for the indicator variable Got to
end of survey. In addition to being zero for cases of attrition, the variable Got to end of
survey will take on the value of 0 if the survey response is deemed to be of insufficient
quality (e.g. where the respondent gave nonsense answers to questions that required
a typed response, or when the total time to complete the survey was too little to have
permitted anyone to have read the questions with sufficient attention to provide an
informed response (i.e. less than 7.5 minutes to complete the survey).
Complete, the dependent variable for the LASSO equation, is a binary indicator
variable that takes on the value of 0 if the respondent does not complete the survey or if
they complete the survey in less than 7.5 minutes. Our response rate, complete surveystotal surveys , is
64%.25
23We conduct our LASSO estimation using the “glmnet‘’ package as implemented in R.24.
25The average completion time in the soft launch of the survey was 15 minutes. Anyone who completed
the survey in less than half of the average completion time (i.e. 7.5 minutes) was determined a "speeder"
and their response was considered invalid on the grounds that they were not providing thoughtful responses.
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Table D1 shows the descriptive statistics for the available explanatory variables
that LASSO methods determine to be relevant in predicting people’s propensities to
respond to the survey. The variables shown were retained by LASSO estimation either
individually or as part of a pairwise interaction. The first row, Outcome: 1=Got to the end
of the survey, is the response rate for this survey. This relatively high response rate, about
65%, may reflect Oregonians’ strong feelings (both positive and negative) toward climate
policy. Rows 1=Gender female through 1=Used a mobile device represent information
collected by the survey for all individuals who make it through the screening process.
The variables in the subsequent rows are for the respondent’s ZIP code (Census ZCTA),
county, or other geographic proximity.
Table D1. Descriptive statistics: response/non-response
models)
Individual explanatory variables used in response/non-
response models (retained by LASSO estimation either
individually or as part of a pairwise interaction term
mean sd
Outcome: 1=Got to end of survey 0.644 0.479
1=Gender:Not male 0.547 0.498
1=Gender:Male 0.453 0.498
1=Own age:18 to 24 0.129 0.336
1=Own age:25 to 34 0.247 0.431
1=Own age:35 to 44 0.174 0.379
1=Own age:45 to 54 0.112 0.315
1=Own age:55 to 64 0.132 0.338
1=Own age:65 and up 0.206 0.405
1=Own age:75 and up 0.058 0.234
1=Own hhld inc:100-125K 0.121 0.327
1=Own hhld inc:150-175K 0.029 0.167
1=Own hhld inc:175-200K 0.020 0.139
1=Own hhld inc:220K up 0.040 0.197
1=Own hhld inc:30-50K 0.127 0.333
Continued on next page
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Table D1 – continued from previous page
1=Own hhld inc:50-75K 0.204 0.403
1=Own hhld inc:75-100K 0.133 0.339
1=Own hhld inc:lt 20K 0.142 0.349
1=Race:Black 0.041 0.199
1=Race:White 0.834 0.372
1=Started survey on Fri 0.119 0.324
1=Started survey on Mon 0.187 0.390
1=Started survey on Sat 0.183 0.387
1=Started survey on Sun 0.177 0.382
1=Started survey on Thu 0.102 0.303
1=Started survey on Wed 0.121 0.327
1=Used a mobile device 0.678 0.467
CDC SVI cnty-Hsg type, transp. 0.747 0.213
County pr: Dial-up internet 0.003 0.002
County pr: Internet w/o subsc. 0.025 0.012
County pr: No internet 0.065 0.033
County pr: Other internet 0.010 0.011
County pr: Satellite internet 0.047 0.026
Dist. nearest wildfire 2010-19 93608.087 51393.059
Dist. nearest wildfire 2020 0.268 0.179
Sq. miles; nearest wildfire 2020 71.629 118.484
ZCTA pr:Asian 4.554 4.938
ZCTA pr:Black 1.978 2.547
ZCTA pr:Other race 3.014 2.855
ZCTA pr:Two or more races 4.913 1.813
ZCTA pr:Below poverty line 0.127 0.093
ZCTA pr:Inc gt 1.5 pov. level 0.780 0.089
ZCTA pr:Income 35 to 50K 0.126 0.021
ZCTA pr:Indus:Arts/ent. 9.926 3.490
ZCTA pr:Indus:Profsci. 11.099 4.197
ZCTA pr:Indus:Publ. adm. 13.902 5.188
ZCTA pr:Indus:Transp. 4.392 1.848
ZCTA pr:Indus:Wholes. 2.663 1.245
ZCTA pr:Internet access 86.081 5.328
ZCTA pr:Live in rural area 0.155 0.238
Observations 1630
B.4.1.2 Probit selection model. LASSO methods are used to identify a set
of regressors that have good out-of-sample predictive ability. We use these variables in
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a probit model to estimate response propensities for a model that uses the explanatory
variables (levels and interactions) that are retained by our LASSO models, where these
variables are summarized in Table D1).
B.4.2 Selection Correction Strategy. Our sample-selection correction
method is an ad hoc two-step model that does not attempt to take into account any
additional unobserved heterogeneity that may account for non-random selection into
the respondent sample. We use an ordinary binary probit specification, with our full
sample of 1630 invited participants, to explain whether each invited participant submits
a completed survey. The fitted probit “index” (the linear combination of estimated
probit parameters and explanatory variables) can be interpreted as a latent respondent
characteristic called “propensity to complete this survey." We calculate the fitted
completion propensity for every invited participant and calculate the mean fitted response
propensity across all of these invitees. We then subtracting this mean from each fitted
individual propensity. The “de-meaned response propensity” (dm : R̂Pi) will therefore be
zero among the full set of 1630 invited participants.
Suppose the set of respondents who complete the survey are all as likely to
provide a a complete and valid response as the overall pool of invited participants.
Then we would expect that the mean response propensity among those who complete
the survey would also be zero. However, in this case, the average person contributing a
completed survey has a greater response propensity than the average in the pool of invited
participants. It is possible that people who are more likely to respond to a survey about
cap-and-trade programs for carbon emissions are simultaneously likely to be willing to
pay more for these programs. If this is the case, our models will tend to overestimate
average WTP in the general population.
If we assume that preferences across cap-and-trade programs can differ
systematically according to response propensities, we can simply allow the fitted response
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propensity to shift each marginal utility parameter in the program choice model.26 We
can then simulate what the preference parameters would have been, had every person
among the invited participants been equally likely to complete a survey, with a response
propensity equal to the average response propensity among all invited participants.
Specifically, we simulate the preference parameters that would obtain if the demeaned
response propensity for each person in the sample of completed responses had been zero.
Unlike a conventional Heckman two-step correction method, this ad hoc
procedure relies upon a wide variety of observable characteristics of the set of invited
participants (or their neighborhoods) to explain response propensities. Unlike the
Heckman correction method, there is no assumption of a truncated bivariate normal joint
distribution for errors in the response/non-response model and the outcome model.
The variables selected by LASSO are thus used to estimate the probit model
shown in Table D2, and the fitted model is used to calculate a response propensity
for each person in the sample of eligible respondents (recall those who cleared the
screening process to the point of encountering the subject of the survey are eligible. We
subtract from each individual’s response propensities our estimate of the mean response
propensity in the eligible group. In the Figure D1, we plot the distribution of these
response propensities for the entire set of invited participants and for the subset of invitees
who completed the survey with responses that passed our basic quality assessment. In the
kernel density for each group, we include vertical lines at zero for the “eligible” group,
and at the mean (0.073) of the de-meaned response propensity when the sample is limited
to just the respondent group.
26As in two-stage-least-squares estimation using least squares methods, it is important that there be at
least some “instruments” for response propensity that do not also enter directly into the utility function
being estimated at the core of the analysis.
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Table D2. Binary probit parameter estimates for selection model
Regressors selected by LASSO methods from a much larger inventory of potential explanatory
variable at the individual, ZCTA, and county level; lambda = min
Estimate
Outcome: 1=Got to end of survey
(1=Gender:Not male) × (1=Race:Black) -0.502∗∗ (0.211)
(1=Gender:Not male) × (1=Started survey on Fri) -0.354∗∗ (0.149)
(1=Own age:18 to 24) × (1=Gender:Male) -0.318∗∗ (0.154)
(1=Own age:18 to 24) × (ZCTA pr:Asian ) -0.0380∗∗∗ (0.0131)
(1=Own age:25 to 34) × (1=Gender:Not male) -0.0280 (0.115)
(1=Own age:25 to 34) × (1=Started survey on Sun) -0.133 (0.181)
(1=Own age:25 to 34) × (1=Started survey on Thu) -0.189 (0.213)
(1=Own age:25 to 34) × (ZCTA pr:Black ) -0.0135 (0.0252)
(1=Own age:35 to 44) × (1=Started survey on Fri) 0.0902 (0.229)
(1=Own age:55 to 64) × (1=Started survey on Thu) 0.113 (0.306)
(1=Own age:55 to 64) × (1=Started survey on Wed) -1.010∗∗∗ (0.361)
(1=Own age:55 to 64) × (Dist. nearest wildfire 2020) -0.524 (0.388)
(1=Own age:55 to 64) × (ZCTA pr:Other race) 0.0440 (0.0361)
(1=Own age:65 and up ) × (1=Started survey on Wed) -0.631∗∗∗ (0.242)
(1=Own age:75 and up ) × (Sq. miles; nearest wildfire 2020) -0.00164 (0.00110)
(1=Own hhld inc:100-125K) × (1=Own age:25 to 34) -0.342∗ (0.207)
(1=Own hhld inc:150-175K) × (1=Started survey on Fri) 0.0138 (0.449)
(1=Own hhld inc:150-175K) × (1=Started survey on Mon) 0.422 (0.747)
(1=Own hhld inc:150-175K) × (1=Started survey on Sat) -0.596 (0.909)
(1=Own hhld inc:175-200K) × (1=Started survey on Wed) -0.286 (0.780)
(1=Own hhld inc:220K up) × (1=Own age:65 and up ) -0.204 (0.361)
(1=Own hhld inc:30-50K) × (1=Own age:35 to 44) -0.0979 (0.246)
(1=Own hhld inc:30-50K) × (1=Started survey on Sat) 0.0588 (0.211)
(1=Own hhld inc:30-50K) × (1=Started survey on Thu) 0.0933 (0.289)
(1=Own hhld inc:30-50K) × (ZCTA pr:Indus:Profsci.) -0.0118 (0.0103)
(1=Own hhld inc:50-75K) × (1=Started survey on Wed) 0.443 (0.280)
(1=Own hhld inc:75-100K) × (1=Own age:45 to 54) 0.149 (0.240)
(1=Own hhld inc:75-100K) × (ZCTA pr:Below poverty line) -1.129∗ (0.603)
(1=Own hhld inc:lt 20K) × (1=Started survey on Wed) -0.412∗ (0.214)
(1=Race:White) × (1=Used a mobile device) -0.0247 (0.0868)
(1=Started survey on Mon) × (ZCTA pr:Indus:Arts/ent.) -0.00482 (0.0154)
(1=Started survey on Mon) × (ZCTA pr:Indus:Publ. adm.) -0.00749 (0.0110)
(County pr: Internet w/o subsc.) × (CDC SVI cnty-Hsg type, transp.) -3.052 (4.030)
(Dist. nearest wildfire 2010-19) × (County pr: No internet) 0.0000111 (0.0000265)
(Dist. nearest wildfire 2010-19) × (County pr: Satellite internet) 0.0000324 (0.0000335)
(Dist. nearest wildfire 2020) × (County pr: Dial-up internet) 51.65 (74.24)
(ZCTA pr:Black ) × (1=Started survey on Fri) 0.0207 (0.0351)
Continued on next page
245
Figure D1. Demeaned response propensities
Table D2 – continued from previous page
(ZCTA pr:Black ) × (ZCTA pr:Live in rural area) 0.683∗∗∗ (0.238)
(ZCTA pr:Inc gt 1.5 pov. level) × (ZCTA pr:Income 35 to 50K) 1.861 (4.859)
(ZCTA pr:Income 35 to 50K) × (ZCTA pr:Internet access) -0.0205 (0.0514)
(ZCTA pr:Income 35 to 50K) × (ZCTA pr:Two or more races) 0.0268 (0.159)
(ZCTA pr:Indus:Transp.) × (County pr: Other internet) 0.708 (0.891)
(ZCTA pr:Indus:Wholes.) × (1=Used a mobile device) -0.106∗∗∗ (0.0268)
Constant 0.563∗∗ (0.221)
Max. log-likelihood -1002.23
No. respondents 1630
Note: Standard errors in parentheses; ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001
246
B.5 Appendix: Choice Experiment Randomizations
Unique Choice Tasks
Each choice task table (e.g. Program A) is populated with values randomly
generated according to a set of parameters. There is no correlation in values between
any of the individual surveys or across any of the six choice tasks within each survey.
With 1000 respondents and 6 choice tasks per respondent there are a total of 6000
independently generated choice task tables.
Value Generation Parameters
We populate the choice task tables (hypothetical carbon cap-and-trade programs)
with values from a structured randomized data generation process. This process
emphasizes both realistic hypothetical carbon cap-and-trade programs and a distribution
of values with enough granularity and orthogonality to allow for precise estimation. All
6,000 programs in the survey (6 programs per respondent times 1000 respondents) are
independently generated. There are nine program features and each of these nine features
is included in every program. Individual features are determined according to their own
specific process. Some of the processes are interdependent, but a degree of random noise
of independence is present in each process to avoid too much collinearity across variables.
The only attribute values that are specific to Oregon in the choice tasks are the carbon
jobs lost and carbon jobs gained, and these values can be fairly easily modified for other
geographic locations. The processes can be seen below.
1. Carbon Reduction Values:
Carbon reduction values are independently drawn with replacement from a uniform
distribution: 10, 20, 30, 40, 50, 60, 70, 80. We believe that this distribution gives
us enough granularity for estimation while also allowing respondents to easily
247
understand the amount of carbon reduction a program will accomplish. These
values are presented as percent reductions achieved by 2050 relative to current
emission levels.
2. Jobs Values
Carbon Jobs Lost and Green Jobs Gained were independently drawn from the
following distribution:
Value ∈ {0.01, 0.02, 0.03, 0.04, 0.05, 0.06, 0.08, 0.10, 0.15, 0.25, 0.30}
Probability ∈ {0.02, 0.10, 0.11, 0.13, 0.20, 0.15, 0.11, 0.09, 0.05, 0.03, 0.01}
Where value indicates the value drawn from the distribution and probability
indicates the value of drawing the corresponding value. For example, there is a
13% chance of drawing 0.04. The draws for both types of job (carbon and green)
were drawn independently and with replacement. These values are generated
to reflect percent of jobs lost (gained) as the result of a cap-and-trade program.
These values are then uploaded into the survey. However, the values that populate
the choice task tables that respondents see are modified. The values that actually
populate the tables are the product of these randomly generated values and the
current level of jobs in the county in which the respondent resides. For instance,
if for a respondent i Program A’s green jobs gained draw took on the value of 0.06
and respondent i indicated they lived in Multnomah County (327,000 current green
jobs) then the value respondent i would see in the Program A table for green jobs
gained would be 0.06∗327,000 = 19,620 jobs. For respondent i Program B’s green
jobs gained draw took on the value of 0.01 then the value respondent i would see in
248
Figure E1. Distribution of job loss randomizations
the Program B table for green jobs gained would be 0.01 ∗ 327,000 = 3,270 jobs.
Below is the distribution of generated values used in the survey with N = 10,000.
3. Share of Permits Auctioned Values:
The share of permits auctioned are independently drawn with replacement from a
uniform distribution: 10, 20, 30, 40, 50, 60, 70, 80. These values are presented as
the percent of total permits in the cap-and-trade program that would be auctioned,
with the remainder being given away to firms at no cost. In some cap-and-trade
programs the percent of permits auctioned will increase overtime. However,
including this dynamic process in the survey is likely to overwhelm respondents
so we simplified the process by suggesting the percent of permits auctioned is static
throughout the existence of the program. The lower bound of 10% was chosen so
that the revenue auction uses are always relevant. The upper bound of 80% was
249
chosen to reflect the reality of how cap-and-trade programs have played out so far.
For instance, there is precedent in the Small Business Regulatory Enforcement
Fairness Act (SBREFA) that some of the permits must be allocated free of charge,
so as not to cause excessive financial burden.
4. Permit Auction Revenue Uses:
There are three potential uses for auction revenues: purchase or subsidize cleaner
equipment for households and firms, support workers and communities that are
disproportionately burdened by program costs, and reduced Oregon taxes.
(a) Clean equipment: values are drawn independently from uniform distribution:
equipmenti ∈ {0,10,20,30,40,50,60,70}.
(b) Support for workers and communities: values are drawn independently from
uniform distribution: supporti ∈ {0,10,20,30,40,50,60,70}.
(c) Tax Reduction: the values for tax reduction are determined by the values for
the preceding two revenue use values. Tax value for instance i is calculated
by 100 − equipmenti − supporti. If this value is negative for a generated
program that program is filtered out of the randomizations pool. The process
guarantees that the three auction revenue uses sum to 100 as well as non-
negative values for the tax feature. Because the equipment values and support
values both have a mean of value of 35 the tax values have a mean of 30. We
are willing to accept this slight imbalance to guarantee respondents see clean
round numbers in the program tables.
5. Additional Regulations On Other Pollutants Values:
250
Additional regulation on other pollutants can take on two values: "YES" and "NO."
These values are drawn independently with a 50% chance of either value being
realized. The values are completely orthogonal to all other values in a program.
6. Cost Values:
Cost values are generated according to the following formula:
[
costi =K ∗ 55+βi ∗bene f iti +αi ∗aucti]onedi − γ1i ∗ equipmenti
− γ2i ∗ supporti − γ3i ∗ taxesi +Hi
β ∈ {0.25, 0.5, 1, 2, 3}
α ∈ {0, 1, 2}
γ1 ∈ {0, 0.25, 0.5, 0.75}
γ2 ∈ {0, 0.25, 0.5, 0.85}
γ3 ∈ {0, 0.25, 0.5, 0.85}
H ∈ {−50,150,20}
K = 1.08
Values for cost of the program were expressed in $ per month. As indicated by the
subscripts costi is generated specific to the other relevant values for programi and
these values are scaled by values randomly generated for each programi. In other
words, all 11 variables are regenerated for each program randomization. Logically,
the higher the target emission reduction (bene f it) the higher the cost of the program
so β takes on a positive value. α also takes on a positive value under the rationale
that if permits are auctioned it will increase production costs for firms. This will
251
Figure E2. Distribution of program cost randomizations
raise consumer prices as well as lead to more job loss in carbon-intensive industries.
All of the permit auction revenue use variables (buying new equipment, support
for communities and workers, and reducing taxes) would likely lead to directly or
indirectly to lower costs to individuals. The term H enters the equation as a random
shock to cost as a way to increase orthogonality across programs. K was used to
scale the cost variable up so that respondents were voting affirmative on programs
approximately half of the time. We set a price floor of $20 for every program so
that if the data generation process resulted in any cost > $20 it was filtered from the
randomizations pool.
Below is the distribution of generated values used in the survey with N = 10,000.
252
B.6 Appendix: Descriptive Statistics for Some Basic Variable Relationships
Given the randomizations of the attributes of the cap-and-trade programs offered
to different respondents, it is informative to look at the joint distributions among a variety
of respondent characteristics and some key relationships between these and the way they
interact with the survey.
Figure F1. Descriptive Statistics: Bias by ideology
B.6.1 Relationships among respondent characteristics and attitudes.
B.6.2 Share of "YES" votes for program by category of respondent.
253
Figure F2. Descriptive Statistics: Votes by age
254
Figure F3. Descriptive Statistics: Votes by income
255
Figure F4. Descriptive Statistics: Votes by ideology
256
Figure F5. Descriptive Statistics: Votes by education
257
Figure F6. Descriptive Statistics: Votes by employment
258
Figure F7. Descriptive Statistics: Votes by climate 1
259
Figure F8. Descriptive Statistics: Votes by climate 2
260
Figure F9. Descriptive Statistics: Votes by ancestors
261
Figure F10. Descriptive Statistics: Votes by cost decile
262
Figure F11. Descriptive Statistics: Votes by benefits
263
B.6.3 Share of "YES" votes by aspect of choice task. Recall that each
respondent is asked to consider six different carbon cap-and-trade programs, Program A
through Program F. All choice experiments that offer respondents more than just a single
choice must contend with what happens as the respondent works through a sequence of
choices. The attributes of Program A, unique to each individual, are incorporated into
that individual’s tutorial material as we explain the different groups of program features.
Despite this, respondents may require a “burn-in” period as they get their bearings with
these choice tasks (and potentially develop some personal choice heuristics). As the
respondent works through the six choice tasks, they may also begin to experience fatigue,
which may deplete their cognitive resources. Sometimes, respondents may rally as they
realize they have reached the final choice task.
In this section, all of the figures show the progression in the specified variable as
the individual works through Programs A through F. All of the attributes are randomized,
as explained in Appendix ??. Thus it is something that is going on with the respondent’s
engagement as they work through the six choices that leads to changes in voting patterns,
not any systematic difference in the attributes of the cap-and-trade programs they are
asked to consider.
Attitudes toward climate change policy are known to differ substantially along
partisan lines. Thus we break out these voting patterns across choice tasks by party
affiliation.
264
Figure F12. Descriptive Statistics: Votes by task
265
Figure F13. Descriptive Statistics: Party votes by task
266
Figure F14. Descriptive Statistics: Time on task
Figure F15. Descriptive Statistics: Touches per task
267
Figure F16. Descriptive Statistics: Clicks per task
268
Figure F17. Descriptive Statistics: Cost per task
B.6.4 Identical distributions of program attributes across tasks?.
269
Figure F18. Descriptive Statistics: Benefits per task
Figure F19. Descriptive Statistics: Carbon jobs per task
270
Figure F20. Descriptive Statistics: Green jobs per task
Figure F21. Descriptive Statistics: Auction per task
271
Figure F22. Descriptive Statistics: Equipment per task
Figure F23. Descriptive Statistics: Workers per task
272
Figure F24. Descriptive Statistics: Relief per task
Figure F25. Descriptive Statistics: Regulations per task
273
Figure F26. Descriptive Statistics: Votes by sector
B.6.5 Votes as a function of non-mutually exclusive categories.
274
Figure F27. Descriptive Statistics: Votes by responsibility
Figure F28. Descriptive Statistics: Votes by descendants
275
Figure F29. Descriptive Statistics: Votes by transportation
276
APPENDIX C
CHAPTER 4 APPENDIX
C.1 Online Appendix: Sensitivity Analysis
277
278
Figure A1. Synthetic control difference-in-difference for Oregon background
checks (raw count)
Background check data is Non-private gun sales subset of FBI data. Events that led to changes in gun purchasing behavior (e.g.,
Obama’s election in 2008), are indicated.
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