What a Difference a Datum Makes: Revisiting the Impacts of Cap-and-Trade on Emissions and Environmental Justice

Abstract

A recent article by Danae Hernandez-Cortes and Kyle Meng suggests that the cap-and-trade program in California led to improvements in the degree of environmental inequity in the state, a result that was taken up with some enthusiasm by proponents of carbon pricing. We suggest that their approach is not designed to capture the variation at the heart of the equity debate and show that the results these authors offer may be problematic because of the potential misidentification of which facilities were actually subject to the cap.

INTRODUCTION

Although the issue of cap-and-trade is frequently the subject of fervent ideological debates, a recent article in the Journal of Public Economics, “Do Environmental Markets Cause Environmental Injustice? Evidence from California’s Carbon Market” by Hernandez-Cortez and Meng (hereafter, HCM) rightly notes that the question of whether carbon markets improve or worsen current environmental disparities in exposure is hard to predict from theoretical considerations alone.1

In their article, HCM highlight their introduction of an approach that contrasts pollutants from facilities covered by cap-and-trade with pollutants from a comparable set of noncovered facilities, suggesting that this can better get at the effect of cap-and-trade. They also stress the superiority of air modeling versus proximity analysis to geographically locate effects and suggest that both the comparative strategy and the introduction of air modeling are dual improvements over previous approaches, including work to which we have contributed.2

Using these methods, the authors conclude that carbon markets in California led to a reduction of an environmental justice (EJ) gap, which is defined in this case as the pollution burden from covered facilities impacting what the state labels “disadvantaged communities” (DACs) relative to other communities also affected by the covered facilities. The circulation of these conclusions, particularly those in an early working paper version of this research, found an eager audience among policy makers considering both the renewal of California’s trading regime and new market systems in other states.3

We suggest here two reasons for caution. First, the HCM method estimates a common percentage decrease in pollutants across all covered facilities from cap-and-trade when the point of a market system is to produce a variety of responses. Second, even if that was the right approach to determining the policy effect, HCM’s conclusions may not be reliable because of their misclassification of regulated and nonregulated facilities. As a result, it remains unclear whether the California experience was associated with improvements or deteriorations in EJ metrics.

THE HCM METHOD

One of the issues raised by EJ critics of cap-and-trade is that allowing firms to decide whether to curtail emissions or to pay others to do so (via purchasing allowances) will necessarily lead to uneven geographic reductions.4 Such a geographically differentiated pattern of emissions reduction is actually the intent of a carbon market: one wants to wring efficiency out of imposing greenhouse gas (GHG) standards by inducing some firms who can more easily and cheaply meet reduction goals to do so while allowing others who may face higher mitigation costs to forego (or minimize) such reductions.

HCM do not look at this key issue of facility variation because of market incentives. Rather, they seek to identify the effect of California’s carbon permit system by estimating a common percentage reduction across regulated facilities relative to nonregulated facilities; the resulting predicted changes in relative physical quantities of pollutants are then fed into an air model to generate estimated changes in aggregate pollution disparities between the bulk of California neighborhoods and DACs.

To estimate this average effect, HCM utilize the following difference-in-difference (DID) equation on a panel of covered and noncovered facilities observed before and after the policy implementation (2008–2017, with the first 5 years being pre-policy and the last 5 years post-policy):5 $asinh (Y_{j t}^{p}) = κ_{1}^{p} [C_{j} \times t] + κ_{2}^{p} [C_{j} \times 1 (t \geq 2013) \times t] + ϕ_{j}^{p} + γ_{t}^{p} + μ_{j t}^{p}$ (1)where asinh is an inverse hyperbolic sine (similar to a log but a transformation that can yield a value when the input value is zero), p refers to the pollutant, j refers to facility, $C_{j}$ is an indicator for whether facility j is covered by the cap-and-trade regulation, t is the year, $Φ_{j}^{p}$ is the facility fixed effect, $γ_{t}^{p}$ is a year fixed effect (to control for changing macroeconomic, demand, and technological conditions), $κ_{1}^{p}$ is the differential 2008–2012 pre-trend for the cap-and-trade facilities before the policy actually went into effect, $κ_{2}^{p}$ is the key estimate of the differential trend after 2012 (2013–2017) when cap-and-trade regulations went into effect, and $μ_{j t}^{p}$ is the error term.

While a trend break, $κ_{2}^{p}$ $,$ that is negative would signal some relative improvement to the pre-policy trend, HCM highlight the differential post-trend estimate $(κ_{1}^{p} + κ_{2}^{p})$ in their abstract and in their discussion of the results. They suggest that they find annual reductions from the cap-and-trade policy (netting away the shared year effects captured by their estimate of $γ_{t}^{p}$ , and with impacts relative to facilities not covered by cap-and-trade) over the 2012–2017 period of “9%, 5%, 4%, and 3% for GHG, PM_2.5, PM₁₀, and NOx, respectively, for the average sample regulated facility”.6

While we understand the attraction of a regression approach that can isolate the common “pure” cap-and-trade effect, the point of cap-and-trade is to prompt more reductions where it may be cheaper and, as such, one might place more focus on variation than on the shared effect. Consider an extreme case where we have two facilities, one of which responds to cap-and-trade by reducing its pollution by 10% while another does not reduce its pollution at all. Applying the facility-average of 5% to estimate the effect of cap-and-trade is a curious approach to determining the disparate effects on nearby neighborhoods.

Is this important empirically? HCM’s estimates impose exactly the same annual relative reduction in GHGs (excluding fixed year effects) of about 8.5% all regulated facilities. However, the actual annual reductions over that time period vary enormously across regulated facilities. For example, in their subsample of regulated facilities (with no controls for shared year effects), the average GHG reduction was 1.4% with a standard deviation of 8.8%; moreover, nearly half of facilities actually experienced increases in emissions, and one-fifth of facilities experienced substantial increases in co-pollutant emissions. This suggests a reason to be more interested in the variation than the mean, and perhaps to adopt simpler approaches that look at what actually happened after cap-and-trade at a facility level rather than applying a modeled effect across facilities.7

We would also note the importance of finding a shared post-policy reduction to their findings. HCM define the EJ gap as the “difference in pollution concentrations between disadvantaged and other communities,” with this calculated just for estimated pollution from the treatment facilities.8 Applying a common percentage estimate means that heterogeneity in the predicted physical quantity of abatement will vary by initial size. If initial pollution from cap-and-trade facilities is unequally distributed by race and income (which HCM acknowledge is true in this sample), applying a large common percentage reduction is likely to predict a relatively larger improvement in absolute terms in DACs because they generally start with a higher level of exposure. In short, in their model, as long as the common differential post-trend estimate is negative and pollution is higher in DACs, the estimated EJ gap will close even if in reality the relative disparity experienced by DACs and non-DACs did not improve.

THE HCM CLASSIFICATION OF CAP-AND-TRADE STATUS

This suggests how reliant HCM’s results are on their estimate of a cap-and-trade effect that is both negative and significant enough to confidently use in subsequent air modeling. This, in turn, is highly dependent on accurately identifying the treatment and control groups in the DID regression (equation 1). Unfortunately, HCM misidentify the treatment group.

How could that occur? As HCM explain in a footnote, they took a version of California’s Pollution Mapping Tool (PMT) that covered 2008 through 2015 and then added 2016 and later 2017 data to it in steps. They found that 39 facilities in the full sample “switched” status from regulated to unregulated, or vice versa, in the newly added years of 2016 and 2017. Because their treatment model requires time-invariant regulatory status, they assumed that the previous status in their 2008–2015 data was accurate and reassigned the subsequent data to the prior status.

The issue came to our attention in 2021 when we initially sought to replicate their work. We had downloaded a full dataset in 2020 which had a variable indicating facility-level regulatory status covering the entire 2008–2017 period that was sometimes in disagreement with the HCM-designated status. When we discovered that divergence, we consulted with data providers at the California Air Resources Board (CARB) and researchers at the state’s Office of Environmental Hazards and Health Assessment (OEHHA) to verify our treatment and control assignments.

We took special care to be consistent with the treatment and control groups being used in an analysis of cap-and-trade being undertaken at that time by California’s OEHHA.9 We made this corrected version of the data available to HCM in January 2022, but they choose not to use it. In a report released in February 2022, we showed that they would have obtained quite different results in their estimated effects had they done so.10

How was it possible that HCM’s cap-and-trade designations could differ from more recent designations that were verified by us with state agencies? Our best guess is that one of authors, Kyle Meng, started with data he used for an earlier article that relied on the very first iteration of the PMT.11 But that first version, which was released in 2017, seems to have had a number of data issues with it; by choosing to change the status in the newer data back to what it was in the older dataset, HCM did not account for any status corrections made by the agencies.

There is now available an even newer version of the PMT data. While previous versions of the PMT (including the version we used in our 2022 report) assigned each facility a single unchanging status, there was, in fact, some movement between regulated and unregulated status that occurred over the 2013–2017 period. While this involves a limited number of facilities, the current version of the PMT now indicates which years in 2013–2017 each facility was required to meet cap-and-trade obligations and which years a facility was not.

We use this new version and assign treatment or control status to a facility based on whether the majority of years in the HCM sample in the 2013–2017 period were spent in regulated or unregulated status. This allows us to continue to assign a single status over the whole period a la HCM but make use of the available and updated information.12

SENSITIVITY OF REGRESSION RESULTS TO TREATMENT SPECIFICATION

Does this make a difference? Later, we adopt the data restrictions imposed by HCM by dropping refineries, electricity generators, and larger emitters. The resulting data represent about 5% of the GHGs regulated by the program, raising issues as to the general applicability of the HCM approach, but that is another topic.13

In Table 1, we offer a profile of what happens when we reexamine the treatment and control designations for the 316 facilities in HCM’s main regression for GHGs. As noted in the table, in this subsample, they switched 22 from the status reported in the most recent data they appended to the status they observed in the initial older dataset.

Table 1.

Example of Differences in Treatment and Control Groups

	HCM sample for the GHG regression
HCM sample		Not switched	“Switcher”
HCM control	210	197	13
HCM treatment	106	97	9
Total	316	294	22
HCM sample (dropping 34 “blanks”)		Not switched	“Switcher”
HCM control	176	163	13
HCM treatment	106	97	9
Total	282	260	22
HCM sample (dropping 34 “blanks”)		Corrected control	Corrected treatment
HCM control	176	162	14
HCM treatment	106	9	97
Total	282	171	111

GHG, greenhouse gas; HCM, Hernandez-Cortez and Meng.

A first step to correcting the control and treatment designations requires understanding that HCM’s use of the earliest version of the Pollution Mapping Tool data is the likely cause of another issue. In the 2008–2015 data they initially downloaded, all facilities were tagged with either “Yes” or “No” as the regulatory status. However, in subsequent years, CARB assigned three possible statuses under cap-and-trade—“Yes,” “No,” and “blank”—and updated the previous years accordingly.

What were the “blanks”? There are 34 facilities that reported emissions in the PMT data from 2008 to 2010 but not thereafter. Nearly all of these are biomass or other facilities that were initially required to provide data to the state’s initial GHG inventory but then stopped because they were not subject to the trading regulations that were to come into effect in 2013. They were reassigned from “No” to blank by the agency itself, a fact that HCM would not have been caught by simply appending 2016 and 2017 data to the earlier 2008–2015 data which has them inappropriately listed as “No.” These facilities did not disappear; using data from another source, we found that they largely kept operating and emitting co-pollutants after 2010.14 Because they were never subject to the possibility of a cap-and-trade status (and their departure in the data was generally not because of a shutdown), they should not be assigned to the control group for considering policy impacts and instead should be dropped from the analysis. This leaves us in the second panel of Table 1 with 282 facilities, 22 of which were switched by HCM to an earlier status.

In the third panel of Table 1, we compare the facility status designations for those 282 facilities to the corrected status obtained from the most recent version of the Pollution Mapping Tool as discussed above. As it turns out, all 13 facilities that HCM switched back to the control group actually spent more time over 2013–2017 as a covered facility; of those 13, one spent all 5 years in the covered or treatment group, eight spent 4 of 5 years in treatment, one spent three of 4 years in treatment, and three spent three of 5 years in treatment. There was also an additional facility in HCM’s control group that was re-classified as part of the treatment group by the newest PMT, giving us a total of 14 classified by HCM as part of the control group that were actually part of the covered or treatment group (using the standard of spending the majority of years in a particular status).

Meanwhile, 8 of 9 that were switched by HCM to the treatment group spent more time over the 2013–2017 period in the uncovered or control group; in these eight cases, the facilities spent three of the 5 years in the control group. There was an additional facility that HCM classified in the treatment group that did not spend a majority of years with such a classification and actually never exceeded the GHG threshold at which a reporting emitter incurs a compliance obligation in the cap-and-trade program (i.e., 25,000 metric tons of “included” GHG emissions in a given year) during 2013–2017. This gives us a total of 9 in the HCM treatment group that were not covered and should have been in the control group not the treatment group to which they were assigned by HCM.

To see what impact using the corrected cap-and-trade status has on the results, we start by using the HCM cap-and-trade designations, including counting the “blanks” as “No’s” as they do, and reproduce their Table 1 results, shown in the first column of our own Table 2. We see a sharply downward post-policy trend $(κ_{1}^{p} + κ_{2}^{p})$ for all pollutants, with nearly all estimates denoted as significant (with the exception of SOX which HCM leave out of most of their discussion).

Table 2.

Coefficient Estimates from Four Specifications

	First estimate with HCMtags (HCM, Table 1)	Second estimate(with corrected tags)	Third estimate (with correctedtags and within-unit)	Fourth estimate (with correctedtags, within-unit, CEIDARS data)
Total GHG
Pre-policy trend	0.187 (0.052)^***	0.141 (0.033)^***	0.133 (0.030)^***
Post-policy break	−0.297 (0.077)^***	−0.179 (0.055)^***	−0.175 (0.058)^***
Post-policy trend	−0.111 (0.036)^***	−0.038 (0.034)	−0.042 (0.041)
# of observations	2,054	1,957	1,208
# of facilities	316	282	135
# of C&T facilities	106	111	90
PM_2.5
Pre-policy trend	0.058 (0.043)^#	0.057 (0.045)	0.053 (0.039)^#
Post-policy break	−0.097 (0.048)^*	−0.072 (0.051)^#	−0.064 (0.043)^#
Post-policy trend	−0.039 (0.018)^**	−0.015 (0.018)	−0.010 (0.024)
# of observations	1,968	1,869	1,177
# of facilities	302	268	130
# of C&T facilities	104	107	88
PM₁₀
Pre-policy trend	0.083 (0.033)^**	0.086 (0.034)^**	0.085 (0.031)^**	0.034 (0.019)^*
Post-policy break	−0.117 (0.040)^***	−0.090 (0.042)^**	−0.088 (0.038)^**	−0.041 (0.038)
Post-policy trend	−0.034 (0.018)^*	−0.004 (0.017)	−0.003 (0.021)	−0.007 (0.025)
# of observations	1,968	1,869	1,177	2,498
# of facilities	302	268	130	256
# of C&T facilities	104	107	88	94
NOx
Pre-policy trend	0.075 (0.039)^*	0.056 (0.040)^#	0.024 (0.035)	0.020 (0.025)
Post-policy break	−0.104 (0.050)^**	−0.056 (0.046)	0.019 (0.055)	−0.032 (0.034)
Post-policy trend	−0.029 (0.019)^#	0.000 (0.018)	0.043 (0.038)	−0.012 (0.019)
# of observations	1,970	1,871	1,177	2,482
# of facilities	303	269	130	255
# of C&T facilities	104	107	88	94
SOx
Pre-policy trend	0.006 (0.035)	0.006 (0.032)	0.005 (0.036)	0.018 (0.023)
Post-policy break	−0.037 (0.043)	−0.033 (0.045)	−0.030 (0.056)	−0.035 (0.032)
Post-policy trend	−0.031 (0.019)^#	−0.026 (0.023)	−0.025 (0.027)	−0.016 (0.025)
# of observations	1,965	1,866	1,174	2,445
# of facilities	303	269	130	251
# of C&T facilities	104	107	88	90

***

Significant at the 0.01 level.

Significant at the 0.05 level.

Significant at the 0.10 level.

Significant at the 0.20 level.

GHG, greenhouse gas; HCM, Hernandez‐Cortez and Meng.

In the second column of Table 2, we use the cap-and-trade designations that came from the process described in Table 1: we exclude the 34 facilities that were “blanks” and assign facilities on the basis of spending the majority of the time period in one status of the other. As can be seen, we obtain quite different results on the post-policy trends.

For example, the estimated annual reduction of GHG from cap-and-trade (net of the fixed year effects) changes from HCM’s estimated 9% to 3%, a result more in line with the fact that the overall cap was set to decline 2% per year in the first period covered (2013–2014) and 3% per year in the second period covered (2015–2017).15 Meanwhile, the annual percentage reductions in PM_2.5, PM₁₀, and NOx—the co-pollutants of real interest to EJ advocates—shift from an annual decline of 5% estimated by HCM to a decline of 2%, from a decline of 4% estimated by HCM to a decline of 1%, and from a decline of 3% estimated by HCM to a flatlining 0%.16

Moreover, with the corrected control and treatment groups, none of the coefficient estimates for the post-policy trends are significantly different from zero. Of the co-pollutants, only PM₁₀ has any trend estimates that come near conventional definitions of significance, making all these estimates with the corrected treatment and control groups less reliable as inputs for the air modeling step of HCM’s strategy.

Our next regression, reported in Column 3 of Table 1, explores another issue. While not explicitly noted by HCM, they do not require both pre and post observations for a facility: of the 316 facilities for GHGs in their Table 1, only 135 have facility-specific data on both sides of the policy break. HCM have suggested that estimating trends in an unbalanced panel might not be problematic if entry and exit is random.17 However, the pattern seems decidedly nonrandom: 34 facilities fall out of their subsample in 2011 (these are the “blanks” that stopped reporting), 97 facilities appear in 2012, and another 49 start reporting in 2013, mostly because of shifts in reporting requirements.18

One reasonable robustness test would be to see what happens when one limits the sample to the 135 facilities that have observations on both sides of the trend break. When we do that and use the corrected cap-and-trade designations from the most recent version of the PMT, the estimated trends are, with the exception of NO_x, somewhat similar to the results in column 2 of Table 2, suggesting that working with an unbalanced panel may not be too problematic.

We also try another reasonable approach to testing the sensitivity of requiring within-unit reporting. The PMT from which HCM draw their data combines GHGs from one reporting source and co-pollutants from another, specifically the California Emissions Inventory Development and Reporting System (CEIDARS). We directly obtained data from CEIDARS for the years 2008 to 2017 and matched it in with the facilities in the PMT. We were able to link in nearly all the facilities with one set of exceptions: the PMT includes a select number of oil and gas emitters that are really reporting entities for satellite emitters at multiple, highly dispersed locations.19

The underlying CEIDARS data provide more precise and longer duration accounting for three co-pollutants, PM₁₀, NOx, and SOx, for both the pre-policy and policy periods.20 The pattern of entry and exit from the data is also more plausibly random: of the 256 facilities in a PM₁₀ regression for the HCM size- and sector-constrained sample, 231 start in 2008 and end in 2017, and the rest of the series begin and end in other years without the bunching of exits in 2010 and entries in 2012 and 2013 that are seen in the HCM regressions.

We show the results in the fourth column of Table 2. Note that the number of facilities included now is close to those in the second column—that is, we have quite good coverage for the co-pollutants even when we require within-unit observations from before and after the policy was implemented. The results again suggest a relative post-policy trend that is far more muted than what HCM offer in their work. Specifically, only one of the coefficients for any relative trend (and this for the pre-policy period) attains even marginal significance in this subsample, and so caution about plugging estimates into an air model remains warranted.

CONCLUSION

HCM have advanced the field with a two-step process that includes air modeling to determine which neighborhoods are affected by changes in pollution. However, the bulk of HCM’s empirical conclusions depend on whether assuming a common percent effect is a reasonable approach to examining the relative burden in communities and whether they have correctly identified the control and treatment groups in the first step of their analysis.

This note stresses the latter issue, pointing out how the results shift when we use a control and treatment identification based on the most recent data from regulatory agencies. However, we remain concerned about applying a common percentage when the point of a cap-and-trade system is to, well, trade. Approaches that focus on the variation have found mixed EJ impacts from cap-and-trade, partly depending on whether one is looking at percentage or quantity reductions, which co-pollutants are the focus, and what time periods are considered.21 In this sense, the jury is still out on the EJ impacts of cap-and-trade in California and more research is warranted.

One could use regression analysis to more directly test variation. For example, Currie et al. use a “triple difference” regression approach to look at the impact of the Clean Air Act on PM_2.5 that takes into account race.22 Sheriff also interacts cap-and-trade status with the percent of people of color living “downwind” of emitters and offers evidence of relative improvements for modeled toxic emissions from cap-and-trade polluters in communities of color in California, although this result is for a very limited number of facilities.23

HCM note in their conclusion—and we heartily agree—that market-based approaches will not necessarily improve (or worsen) EJ gaps, and so EJ-specific policies must be put in place.24 Careful market design could help ameliorate some reasonable concerns about the environmental and social inequities that can result from carbon pricing.25 For example, there is now some interest in facility-specific caps as one way to limit unwanted side effects, an approach that bears some similarity to a selective “no trading zone” strategy we proposed at the beginning of California’s cap-and-trade regime.26 This may be a promising area for both new research and new policy development.

Footnotes

ACKNOWLEDGMENTS

The authors thank Kyle Meng and Danae Hernandez-Cortes for productive and cordial exchanges about the underlying data and analytical issues and choices; Álvaro Alvarado, Laura Plummer, and Amy Budahn from California’s Office of Environmental Health Hazard Assessment as well as staff at the California Air Resources Board for assistance with understanding and verifying the data; Lara Cushing, Rachel Morello-Frosch, and Jim Sadd for their collaboration on the project that lifted up the issues we tackle in this article; Danny Cullenward for his comments and assistance in understanding both data and policy implications; James Boyce, Deepankar Basu, Charles Komanoff, Suresh Naidu, Gregor Semieniuk, and participants in the University of Massachusetts, Amherst Applied Micro Workshop for their comments on this work; and Bridget Diana, Edward Muña, and Justin Scoggins for research assistance.

AUTHORS’ CONTRIBUTIONS

The ordering of the authors is alphabetical. Both authors contributed to methodology and writing, with M.A. making especially important contributions to conceptualization. M.P. was responsible for data cleaning, software coding, and formal analysis and did the bulk of the writing.

AUTHOR DISCLOSURE STATEMENT

No competing financial interests exist.

FUNDING INFORMATION

No funding was received for this article.

1

Danae Hernandez-Cortes and Kyle C. Meng, “Do Environmental Markets Cause Environmental Injustice? Evidence from California’s Carbon Market,” Journal of Public Economics 217 (January 2023): 104786.

2

Lara Cushing et al., “Carbon Trading, Co-Pollutants, and Environmental Equity: Evidence from California’s Cap-and-Trade Program (2011–2015),” PLOS Medicine 15, no. 7 (July 10, 2018): e1002604; Laurel Plummer et al., “Impacts of Greenhouse Gas Emission Limits Within Disadvantaged Communities: Progress Toward Reducing Inequities” (Sacramento, CA: Office of Environmental Health Hazard Assessment, February 2022).

3

Danae Hernandez-Cortes and Kyle Meng, “Do Environmental Markets Cause Environmental Injustice? Evidence from California’s Carbon Market,” NBER Working Paper 27205 (UC Santa Barbara: National Bureau of Economic Research, 2020), <>

4

For an early examination of this issues, see Stephen P. Winslow, “Transplanting Emissions Trading to Interstate Areas: Will It Take Root?,” Pace Environmental Law Review 5, no. 1 (September 1, 1987): 297.

5

Hernandez-Cortes and Meng, “Do Environmental Markets Cause Environmental Injustice?,” 6.

6

Ibid., 10. HCM’s specific formula, which we adopt in our own calculations, takes the percent change in the detrended prediction of a pollutant between 2012 and 2017, and divides by 5.

7

HCM do acknowledge the limits of imposing a common percentage effect and so introduce a robustness test in which the cap-and-trade differential trend estimates vary by the initial pollution level of the facility. This is not necessarily a good test of the EJ concern: for facilities HCM designate as cap-and-trade in the subsample used in their primary regression for which we were able to link average CalEnviroScreen scores within five miles, the correlation between HCM’s preferred size metric (average annual metric tons of GHGs) and that CalEnviroScreen measure is .0017, with a significance level of .9872, essentially a finding of no relationship.

8

Ibid., 7.

9

Plummer et al., “Impacts of Greenhouse Gas Emission Limits Within Disadvantaged Communities: Progress Toward Reducing Inequities.”

10

Manuel Pastor et al., “Up in the Air: Revisiting Equity Dimensions of California’s Cap-and-Trade System” (Los Angeles, CA: USC Equity Research Institute, February 2022), <>

11

Kyle C. Meng, “Is Cap-and-Trade Causing More Greenhouse Gas Emissions in Disadvantaged Communities?,” in DISTRIBUTIONAL EFFECTS OF ENVIRONMENTAL MARKETS: INSIGHTS AND SOLUTIONS FROM ECONOMICS, ed. Christopher J. Costello (Bozeman, MT: Property and Environment Research Center, 2019), 27–31.

12

One reviewer suggested experimenting with allowing the status to change over years rather than assuming a single status. While a useful next step, our focus here is on replication and illustrating the misidentification issue—and to replicate HCM, we also need to estimate a pre-policy trend that is invariant by subsequent status. Moreover, as noted in the text, we think a simpler approach focused on variation would get at the policy debate more effectively.

13

In a previous working paper, we raised concerns about applicability over the whole sample. However, HCM has not included the full dataset in the official replication data they have made available and have requested that we confine our attention to that more limited data; as a result, we cannot fully portray the results when one estimates outside their subsample.

14

Of the 34 facilities in the HCM subsample that stopped reporting GHG emissions to the PMT, 30 can be linked to a co-pollutant database we describe later, with 27 of those having co-pollutant observations, and 25 of those have co-pollutant data that stretches to 2015 or 2017.

15

See <https://www.c2es.org/content/california-cap-and-trade>

16

The observant reader might wonder how a coefficient value for the post-policy trend of -.038 for total GHGs translates to a percentage annual relative decrease of 3% (or how in HCM’s regression, a post-policy trend of -.111 translates to a 9% relative reduction per annum); that is, why do these trend estimates differ from the coefficient estimates in that helps to generate them? This is partly due to the use of the inverse hyperbolic sine specification, a strategy that allows the inclusion of observations that are zero but which yields coefficients not as straightforwardly applicable as coefficients from a regression with a log-transformed dependent variable; see John Mullahy and Edward C. Norton, “Why Transform Y? The Pitfalls of Transformed Regressions with a Mass at Zero*,” Oxford Bulletin of Economics and Statistics 86, no. 2 (April 2024): 417–47. Another factor is that we apply HCM’s approach of taking the percent change in the estimated value (after reverse transforming) over five years and dividing by 5; this yields a smaller averaged reduction because applying the same percentage decrease to each year of the five year stretch yields a smaller quantity decrease as the base for each year’s subsequent decline calculation falls in value.

17

Danae Hernandez-Cortes and Kyle C. Meng, “The Importance of Causality and Pollution Dispersal in Quantifying Pollution Disparity Consequences: Reply to Pastor et al. (2022),” April 2022, 9.

18

One additional facility also drops out because it has no observations for 2012. We thank Danny Cullenward for explaining to us the shift in reporting requirements; for more, see <https://ww2.arb.ca.gov/sites/default/files/classic/cc/reporting/ghg-rep/reported-data/2008-2012-ghg-summary-2013-11-04.pdf>

19

A share of the oil and gas facilities in the Pollution Mapping Tool are central reporting entities for multiple emitters that are often a long distance away; see Pastor et al., “Up in the Air: Revisiting Equity Dimensions of California’s Cap-and-Trade System.” HCM assume that the geographic location of these select reporting entities given in the Pollution Mapping Tool is where the emissions are actually released which is generally not the case.

20

PM_2.5 was not easily available as it requires additional processing by state authorities.

21

Dallas Burtraw and Nicholas Roy, “How Would Facility-Specific Emissions Caps Affect the California Carbon Market” (Resources for the Future, July 2023), <https://media.rff.org/documents/Burtraw_and_Roy_-_Facility-Specific_Caps_Comment_for_Posting.pdf>; Pastor et al., “Up in the Air: Revisiting Equity Dimensions of California’s Cap-and-Trade System”; Plummer et al., “Impacts of Greenhouse Gas Emission Limits Within Disadvantaged Communities: Progress Toward Reducing Inequities.”

22

Janet Currie, John Voorheis, and Reed Walker, “What Caused Racial Disparities in Particulate Exposure to Fall? New Evidence from the Clean Air Act and Satellite-Based Measures of Air Quality,” American Economic Review 113, no. 1 (January 1, 2023): 71–97.

23

Glenn Sheriff, “California’s GHG Cap and Trade Program and the Equity of Air Toxic Releases,” Journal of the Association of Environmental and Resource Economists, May 2023. Sheriff connects cap-and-trade and non-cap-and-trade facilities with air-modeled data on toxics taken from the U.S. EPA’s Toxic Release Inventory (TRI) and the Risk-Screening Environmental Indicators (RSEI) model; whether this also applies to other co-pollutants, like PM_2.5, is an open empirical question. By contrast, when we interact a geographic proximity data (a DAC within five miles) with the policy break time trend for the emitters in the HCM sample using the more comprehensive CEIDARS data, we find that interaction variable to be positive although only the results on NOx meet a reasonable level of statistical significance. We do not present those results partly for the sake of brevity but also because proximity metrics can be reasonably criticized as less reliable than plume-based measures, and, in any case, the results are not particularly significant.

24

Hernandez-Cortes and Meng, “Do Environmental Markets Cause Environmental Injustice?,” 15.

25

James K. Boyce, Michael Ash, and Brent Ranalli, “Environmental Justice and Carbon Pricing: Can They Be Reconciled?,” Global Challenges, February 28, 2023, 2200204; Nicky Sheats, “Achieving Emissions Reductions for Environmental Justice Communities Through Climate Change Mitigation Policy,” William & Mary Environmental Law and Policy Review 41, no. 2 (February 15, 2017): 377.

26

Burtraw and Roy, “How Would Facility-Specific Emissions Caps Affect the California Carbon Market”; Manuel Pastor et al., “Minding The Climate Gap: What’s at Stake If California’s Climate Law Isn’t Done Right and Right Away” (Los Angeles, CA: USC Program for Environmental and Regional Equity (now the Equity Research Institute), April 2010), <>