## Abstract

Environmental regulations may cause firms to reoptimize over pollution inputs. By regulating air emissions in particular counties, the Clean Air Act (CAA) gives firms incentives to substitute toward polluting other media, like waterways, and toward pollution from plants in other counties. I test these hypotheses using the EPA Toxic Release Inventory (TRI). Regulated plants increase their ratio of water-to-air emissions by 177% (102 log points) and their level of water emissions by 105% (72 log points). Regulation of an average plant increases air emissions at unregulated plants within the same firm by 11%.

## I. Introduction

ECONOMIC theory predicts firms will respond to environmental regulation by reoptimizing over pollution inputs. In the presence of unpriced or mispriced externalities, such responses can generate outcomes that are inefficient, unintended by policymakers, or both. The Clean Air Act (CAA) regulates particular air pollutants in particular counties, which creates incentives for firms to substitute among different forms of pollution. This paper tests two variants of this hypothesis: (a) Do firms respond to air pollution regulation by polluting other channels, like landfills and waterways [cross-media substitution], and (b) Do multiplant firms substitute toward pollution from less regulated plants [spatial leakage]?

Before testing these predictions, I first evaluate the accuracy of my primary data set, the EPA Toxic Release Inventory (TRI). A strand of previous work, including de Marchi and Hamilton (2006), has identified flaws in these data. I argue that the scope for bias from misreporting is limited given my empirical specifications. Analysis of water emissions data from EPA Discharge Monitoring Reports (DMR) and air emissions data from the National Emissions Inventory (NEI) shows strong correlations with the TRI.

I then proceed to questions of substitution. There is anecdotal evidence of such behavior. Duhigg (2009) describes a power plant that responded to air quality lawsuits by installing smokestack scrubbers, which spray water and chemicals into the stream of exhaust gases. The plant dumped the liquid waste from the scrubbers into the Allegheny River. Previous empirical studies in economics, however, have found little evidence of cross-media substitution. Sigman (1996) tests for substitution in chlorinated solvent releases by metals and manufacturing plants. The author finds no substitution driven by the CAA but does find substitution driven by hazardous disposal prices. Greenstone (2003) tests for CAA-induced substitution in releases from the iron and steel industry and finds no evidence for it. Gamper-Rabindran (2009) models emissions of volatile organic compounds (VOC) by chemical manufacturers as a function of CAA regulation and finds no increased emissions into other media.

My approach builds on this work along several dimensions. Following the implications of Auffhammer, Bento, and Lowe (2009) and Bento, Freedman, and Lang (2014), I first account for spatial heterogeneity in regulation. If one of a county's air pollution monitors exceeds the CAA standard, the EPA designates the county as “nonattainment.” The state then issues regulations to reduce that county's air pollution. I demonstrate that only plants near nonattainment monitors are treated under the CAA.1 My analysis accounts for this and so avoids averaging changes at treated plants with null responses from untreated plants in nonattainment counties. Second, by estimating effects on levels rather than growth rates, I capture long-term responses. I find that treated plants decrease air emissions by 38% (49 log points).

Motivated by a simple theoretical model, I show that one can use emissions ratios to recover the signs of net substitution elasticities among pollution inputs. I evaluate the resulting hypotheses by comparing regulated (“treated”) plants in particulate nonattainment counties to untreated plants. My identification relies on the conditional exogeneity of county nonattainment status and distance to the nearest nonattainment air pollution monitor. I find evidence of both cross-media substitution and spatial leakage. Regulated plants increase their ratio of water-to-air emissions by 177% (102 log points) and their level of water emissions by 105% (72 log points). These effects are large in proportional terms because baseline water emissions at treated plants are low. By mass, the water emissions increase is only 9% of the air emissions decrease at treated plants. Regulation of an average plant increases air emissions at unregulated plants owned by the same firm by 11%, offsetting 37% of a firm's emissions reductions. The latter result recommends caution in studying CAA impacts with difference-in-differences designs.

These findings are important not only for air pollution regulation but for pollution control policy generally. If firms substitute among various forms of pollution, an efficient policy must consider not only a plant's emissions into a particular medium, but rather a firm's emissions across all media, in all locations (Muller & Mendelsohn, 2009). As of this writing, the president has ordered the EPA to rescind or revise two important rules governing water pollution (Biesecker, 2017; Davenport, 2017). These changes have the potential to worsen substantially the unintended consequences of air pollution regulations.

My analysis contributes to the literature on regulation in the presence of mispriced inputs (e.g., Campbell, 1991). To the best of my knowledge, it is the first work to document regulation-induced cross-media pollution substitution. It complements empirical studies of CAA compliance, like Curtis (2018) and Evans (2016). This study also contributes to the literature on pollution leakage (Levinson & Taylor, 2008; Fowlie, 2009; Hanna, 2010; Bushnell & Mansur, 2011) by presenting evidence of unintended emissions leakage across existing domestic plants. Finally, to the best of my knowledge, this is the first study to show spatial heterogeneity in CAA-driven air emissions reductions at the plant level. This finding contributes to the literature on strategic behavior by state regulators (Sigman, 2003, 2005; Grainger, Schreiber, & Chang, 2018).

The rest of the paper is organized as follows. Section II discusses my theoretical model, and section III describes the data. Section IV presents estimating equations, defines treatment, and explores identifying assumptions. Section V discusses results, and section VI explores their robustness. Section VII concludes.

## II. Theory

The following simple model informs my empirical approach. Suppose a firm operates two plants, indexed by $i∈1,2$, producing total quantity $Q=q1+q2$ of a single good. Each plant employs two pollution inputs $Ai$ and $Wi$ and a composite third input, $Li$, comprising labor, capital, land, and so on. For discussion, let $Ai$ be air emissions and $Wi$ be water emissions. The plants are located in different counties and face different input prices $pAi,pWi,pLi$.

Assume that the plant-level cost functions are multiplicatively separable into plant-specific functions of quantity $fi$ and input prices $gi$.2 Then one can write the firm's cost function as follows:
$CQ,pA1,pW1,pL1,pA2,pW2,pL2=f1q1*g1pA1,pW1,pL1+f2q2*g2pA2,pW2,pL2.$
Note that quantities $qi*$ are functions of $Q$ and input prices in both locations. Like any other cost function, $C·$ is homogeneous of degree 1 in input prices. Using Shephard's lemma, one can differentiate to obtain conditional demand for pollution inputs at either plant:
$Wi*=∂C∂pWi=fiqi*∂gi∂pWi+∂fi∂qi*∂qi*∂pWigi+∂f-i∂q-i*∂q-i*∂pWig-i,Ai*=∂C∂pAi=fiqi*∂gi∂pAi+∂fi∂qi*∂qi*∂pAigi+∂f-i∂q-i*∂q-i*∂pAig-i.$
At optimum $∂qi*∂pWi=∂qi*∂pAi=0$, so the second and third terms in the previous expressions vanish:
$Wi*=∂C∂pWi=fiqi*∂gi∂pWipAi,pWi,pLi,Ai*=∂C∂pAi=fiqi*∂gi∂pAipAi,pWi,pLi.$
These input demands are homogeneous of degree 0 in input prices $pAi,pWi,pLi$, so they can be written as functions of price ratios. Dividing yields an optimal input ratio that is independent of output $Q$ and other-plant input prices:
$Wi*Ai*=∂gi∂pWi∂gi∂pAi≡hipAipWi,pAipLi,pLipWi.$
(1)
Under these conditions, then, one can learn about net substitution by estimating the relationship between the optimal input ratio and own-plant prices or price proxies. One need not control for output quantity, as in estimation of translog cost functions (see, e.g., Humphrey & Moroney, 1975, and Westbrook & Buckley, 1990). While this result is well known in the literature on cost functions (Berndt & Christensen, 1973), to the best of my knowledge, it has not previously been applied in environmental economics, where input prices and output are commonly unobserved. Previous pollution substitution work has typically employed a stronger assumption of constant returns to scale (CRS; see, e.g., Fullerton & Karney, 2018).3
For expositional convenience, I will temporarily assume plant-level production is CES. Then $Wi*Ai*=hipAipWi,pAipLi,pLipWi=cWicAipAipWiσi$ (the derivation is in appendix section D.3), where $cAi$ and $cWi$ are technological constants. Taking logs yields the following expression:
$lnWi*Ai*=σilncWicAi+σilnpAipWi.$
(2)
In this case, a single global parameter $σ$ represents the Morishima elasticity of substitution with respect to price $pA$: $σ=MAWQ,pA,pW=ɛWA-ɛAA$, where $ɛWA$ and $ɛAA$ are cross- and own-price elasticities of input demand (Morishima, 1967; Blackorby & Russell, 1989). While this is the natural generalization of the Hicks elasticity, its asymmetry makes it different in one important respect: the elasticity $MAW$ is informative for changes in $pA$ but not for changes in $pW$. The sign of $MAW$ is ambiguous because the sign of $ɛWA$ is unknown when there are three or more inputs. If $MAW$ is positive, the inputs are net substitutes. If it is negative, they are net complements. Given $pApW$ or a suitable proxy, one can recover the sign of the Morishima elasticity. One need not assume CES production. Under the assumption of multiplicative separability in the cost function, one can recover the sign of this elasticity without observing output, but it may be local, rather than global, as in the CES case.

Suppose plant 1 faces CAA regulation, but plant 2 does not. Regulation increases relative input prices $pA1pW1$ at plant 1 through two channels: (a) pecuniary cost (e.g., variable abatement cost) and (b) nonpecuniary cost (e.g., the potential displeasure of a regulator). The model predicts that $W1*A1*$ will respond to CAA regulation, revealing net substitutability or complementarity. It predicts $W2*A2*$ will not respond, as the optimal input ratio at plant 2 is independent of prices at plant 1. The input levels $A2*,W2*,L2*$, however, do depend on prices at plant 1. If $∂f2∂pA1>0$, as is standard, then $∂A2*∂pA1>0$; CAA regulation will reduce air emissions at plant 1 while increasing them at plant 2.4 The equations that come out of this theory are susceptible to empirical attack with contemporary methods for identifying causal effects. As some input prices and outputs may be endogenous, even for a firm that is a price taker with respect to pollution, this approach may be broadly useful. For additional theoretical discussion, see appendix D.

## III. Data

### A. Sources

My plant-level emissions and location data come from the EPA Toxic Release Inventory (TRI). Covered firms self-report annual emissions by mass and chemical using a standardized form. The database also includes the name and Dun & Bradstreet DUNS number of the parent company of each plant. To the best of my knowledge, the TRI is the only data set in which firms report both air emissions and emissions into other media. A subset of TRI chemicals are classified as particulates (PM).5 The TRI data capture emissions in great detail, distinguishing, for example, between different types of underground wells. To simplify presentation and analysis, I aggregate up to the categories described in table A3. In the early years of TRI data collection, reporting requirements changed dramatically (de Marchi & Hamilton, 2006; U.S. EPA, 2012a). To avoid confounding such reporting changes with genuine emissions changes, I exclude the period 1987 to 1991 from my analysis.

Data on county attainment status come from the EPA Green Book, 1992–2014. Monitor-level data on pollutant concentrations come from the EPA Air Quality System (AQS), 1990–2014. My primary merged data set thus runs from 1992 to 2014. (For descriptive statistics, see appendix table A4.)

### B. TRI Accuracy

The self-reported nature of the TRI has led researchers to scrutinize its accuracy (Hamilton, 2005; de Marchi & Hamilton, 2006), and potential misreporting warrants discussion. Time-invariant misreporting would not bias my estimates, as all specifications include plant fixed effects. Similarly, time-varying secular misreporting would not produce bias because my specifications include year fixed effects. Two types of misreporting could yield spurious positive treatment effects on nonair emissions: (a) increased overreporting or decreased underreporting by treated plants simultaneous with treatment or (b) increased underreporting or decreased overreporting by control plants simultaneous with treatment. It is possible to imagine plausible versions of situation (a). Suppose, for example, a plant were underreporting, and that treatment (regulation) halted such underreporting. Treatment would lead to increased reported emissions into all media, but actual emissions would be initially unchanged. My empirical results are inconsistent with the imagined reporting behavior: air emissions do not increase, but rather decrease, and the ratio of water-to-air emissions increases (see section V). A plant would have to differentially underreport water emissions, relative to air emissions, in the pretreatment period to generate this pattern. While I cannot exclude such a scenario, neither the theory of section II nor the regulatory details of section IVB suggest it is reasonable.6 Misreporting of type b) is still harder to credit. Most control plants are located far from a given treated plant. Their managers likely do not know the nature or timing of regulations applied to the treated plant, nor do they have incentives to tie their misreporting to such regulations.

In order to evaluate TRI accuracy directly, I employ an EPA tool that links annual facility-level surface water emissions from the TRI and Discharge Monitoring Reports (DMR), 2007–2015.7 Plants submit DMRs, which are typically based on direct measurements, so that EPA can evaluate compliance with permits issued under the Clean Water Act (U.S. EPA, 2012b). While there is the potential for misreporting, it is mitigated by EPA inspections, during which the agency conducts its own measurements (Helland, 1998b). I subset the merged TRI-DMR data to chemicals classed as particulates when emitted into the air, which are the subject of my primary analysis. Regressions of log DMR surface water emissions on log TRI surface water emissions yield coefficient estimates of .88 to .94 at the facility-year-chemical level and .66 to .85 at the facility-year level (see table 1). All are statistically significant at the 1% threshold. That is, a 1% increase in reported TRI emissions predicts a .66% to .95% increase in DMR emissions. These results are potentially consistent with measurement error in the TRI, but they are also evidence that the TRI contains useful information about water emissions of the chemicals I study. Similarly, I benchmark TRI air emissions against EPA's National Emissions Inventory (NEI). Estimates range from .82 to .897 at the plant-chemical-year and from .61 to .91 at the plant-year level (see table 1). (For a more detailed discussion of the TRI, see online appendix C.)

Table 1.
Comparison of TRI Emissions to DMR (Water) and NEI (Air)
(1) DMR Water(2) DMR Water(3) DMR Water(4) DMR Water(5) DMR Water(6) DMR Water
TRI water 0.876*** 0.876*** 0.939*** 0.852*** 0.853*** 0.658***
(0.0371) (0.0371) (0.0549) (0.0432) (0.0431) (0.0694)
Year FE No Yes Yes No Yes Yes
Plant FE No No Yes No No Yes
Observations 8,364 8,364 8,364 4,197 4,197 4,197
NEI Air NEI Air NEI Air NEI Air NEI Air NEI Air
TRI air 0.894*** 0.897*** 0.820*** 0.910*** 0.912*** 0.614***
(0.0125) (0.0125) (0.0310) (0.0114) (0.0115) (0.0911)
Year FE No Yes Yes No Yes Yes
Plant FE No No Yes No No Yes
Observations 5,945 5,945 5,945 3,952 3,952 3,952
(1) DMR Water(2) DMR Water(3) DMR Water(4) DMR Water(5) DMR Water(6) DMR Water
TRI water 0.876*** 0.876*** 0.939*** 0.852*** 0.853*** 0.658***
(0.0371) (0.0371) (0.0549) (0.0432) (0.0431) (0.0694)
Year FE No Yes Yes No Yes Yes
Plant FE No No Yes No No Yes
Observations 8,364 8,364 8,364 4,197 4,197 4,197
NEI Air NEI Air NEI Air NEI Air NEI Air NEI Air
TRI air 0.894*** 0.897*** 0.820*** 0.910*** 0.912*** 0.614***
(0.0125) (0.0125) (0.0310) (0.0114) (0.0115) (0.0911)
Year FE No Yes Yes No Yes Yes
Plant FE No No Yes No No Yes
Observations 5,945 5,945 5,945 3,952 3,952 3,952

Merged DMR-TRI data on particulates from EPA's DMR Pollutant Loading Tool, 2007–2015. The dependent variable is log water emissions (pounds). All columns include a constant term. SEs are clustered at the plant level (county not available in merged DMR-TRI data from the DMR Reporting Tool). The unit of observation is a plant-chemical-year in columns 1–3 and a plant-year in columns 4–6. National Emissions Inventory (NEI) data from EPA (2008, 2014). The dependent variable is log air emissions (pounds). All columns include a constant term. The unit of observation is a plant-chemical-year in columns 1–3 and a plant–year in columns 4–6. SEs are clustered at the plant level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

## IV. Empirical Strategy and Regulatory Background

### A. Estimating Equations

As outlined in section II, under multiplicative separability, one can model emissions ratios as a function of price ratios to investigate net (Morishima) elasticities of substitution across media. To that end, I estimate the following equation, with $i$ indexing plant and $t$ year:
$lnWitAit=αi+δt+βtreatedit+ɛit.$
(3)
The quantity $lnWitAit$ is the plant's log emissions ratio, with the numerator emissions into another medium (e.g., water or land) and the denominator air emissions. The estimating equation closely parallels the ratio of conditional factor demands from equation (1). The treatment (regulation) dummy, explained in section IVB, proxies for the unobservable increase in the price ratio $pApW$. The coefficient $β=νσ$ is a scalar function of the Morishima elasticity of substitution $σ$, where $ν$ is the percentage increase in relative prices produced by treatment. If air and water emissions are net substitutes, theory predicts the CAA will induce cross-media substitution, and estimates of $β$ will be positive. If, instead, air and water emissions are complements, estimates of $β$ will be negative. The equation includes plant and year fixed effects, with the latter capturing secular forces influencing emissions. I also estimate specifications with county-year and industry-year fixed effects.8

I have assumed that CAA regulation changes relative input prices. This is plausible in part because abatement technologies have large variable costs, ranging from 33% to 100% of capital cost for most abatement technologies (U.S. EPA, n.d.; Vatavuk, van der Vaart, & Spivey, 2000; Farnsworth, 2011). In the case of fossil electric power generation, abatement technologies consume 0.1% to 3% of electricity generated (World Bank Group, 2017). For other abatement options like fuel switching and coal washing, the new fuel must be weakly more expensive than the old, or the plant would have been using it before.

In some policy contexts, the gross change in input demand may be of interest, and I estimate it as follows:
$lnWit=αi+δt+βtreatedit+ɛit.$
(4)

The dependent variable is the log of a plant's emissions into a particular medium (e.g., air or water). If CAA regulations are effective in reducing air emissions, the corresponding estimate of $β$ will be negative. If firms employ cross-media substitution in response and substitution effects dominate output effects, the estimates of $β$ will be positive for other media, like water and landfills.

The theory of section II predicts that firms might respond to treatment of a plant in one county by shifting air emissions to a plant in another county. To test for such within-firm leakage, I estimate the following specification using only plants in attainment counties:
$lnAit=αi+δt+βother_treatedit+ɛit.$
(5)
The variable $other_treatedit$ is a dummy for one or more treated plants within the same firm, year, and industry. If the CAA induces spatial leakage, estimates of $β$ will be positive. Again, I begin with plant and year fixed effects and then add county-year and industry-year fixed effects.

### B. Defining Treatment

The following discussion of CAA regulation is intended to provide the minimum background for the treatment dummy employed in my estimating equations. (For more detail on relevant environmental regulation, see appendix B and Revesz & Lienke, 2016.) Under the CAA, the EPA sets air quality standards for six criteria pollutants, including particulate matter ($PM10$ and $PM2.5$). If at least one monitor in a county exceeds the standard for a particular pollutant, that county is typically considered in violation of the CAA. Throughout this paper, I refer to a monitor that exceeds a CAA standard as a nonattainment monitor. A monitor violation triggers the following sequence (author's interview notes; U.S. EPA, n.d.):

1. Together EPA and the state go through a process to designate a county as nonattainment. This may take up to two years.

2. Nonattainment designation begins a process through which states submit a state implementation plan (SIP) to EPA. This may take 18 to 36 months.

3. SIPs are not federally enforceable until EPA approves them, but state authorities may enforce them prior to such approval. As a result, actual regulation sometimes begins concurrent with a nonattainment designation but often begins after a delay of a year or more.

Research on cross-media substitution has typically defined treatment as presence in a nonattainment county, but this conceals important spatial heterogeneity. Auffhammer et al. (2009) find the effect of county nonattainment status on an average monitor is 0, but the effect on a nonattainment monitor is −11% to −14%. Similarly, Bento et al. (2014) find that nonattainment affects home prices near nonattainment monitors but not farther away. In advance of my empirical analysis, this suggests that regulators treat plants near nonattainment monitors intensively, while treating plants farther away lightly or not at all. To evaluate this prediction, I estimate a simple regression of a plant's air emissions on plant and year fixed effects:
$lnAit=αi+δt+ɛit.$
(6)
In this equation, $A$ denotes air emissions, while $i$ indexes plant and $t$ year.

Figure 1 then uses residuals from this regression to examine spatial heterogeneity. In both panels, I estimate a local linear regression of residual log air pollution on the distance to the nearest nonattainment monitor. The upper panel uses a control sample: attainment plant-years in counties that later fall into nonattainment. It shows that plants near the (future) nonattainment monitor are above their long-run average emissions. The lower panel uses a treatment sample: plants in counties that were in nonattainment in the previous year and so could have been regulated. Residuals are large and negative (roughly −50 log points) near the nonattainment monitor, indicating air emissions abatement. As distance to the monitor increases, the residuals rapidly rise to 0 near 1 kilometer and remain there. Figure 1 provides evidence that regulators indeed treat plants near nonattainment monitors intensively, while treating more distant plants lightly or not at all.

Figure 1.

Air Emissions by Distance from Nearest Nonattainment monitor

Underlying residuals from equation (6), a panel model of log on-site air emissions (in pounds) with plant and year fixed effects. The fitted lines come from local linear regressions. The shaded area is the 95% confidence interval. The 25th percentile of the distance distribution is 3.8 kilometers. In the upper panel, the sample is limited to plant-years from eventual nonattainment counties prior to the first nonattainment designation. In the lower panel, the sample is limited to plants in counties that were in nonattainment in the previous year.

Figure 1.

Air Emissions by Distance from Nearest Nonattainment monitor

Underlying residuals from equation (6), a panel model of log on-site air emissions (in pounds) with plant and year fixed effects. The fitted lines come from local linear regressions. The shaded area is the 95% confidence interval. The 25th percentile of the distance distribution is 3.8 kilometers. In the upper panel, the sample is limited to plant-years from eventual nonattainment counties prior to the first nonattainment designation. In the lower panel, the sample is limited to plants in counties that were in nonattainment in the previous year.

Based on this pattern, I define a variable $treatedit=Nonattainit-1×1Distanceit-1⩽D¯$. That is, I consider a plant treated in year $t$ if in the prior year, its county was in nonattainment and the plant was located “close” to a nonattainment monitor. A nonattainment monitor is one that violated the CAA $PM10$ or $PM2.5$ standards in year $t-1$ or previously. Based on figure 1, I use a threshold distance $D¯$ of 1.07 kilometers, the distance at which I can no longer reject a null hypothesis of a 0 treatment effect on air emissions (at the 5% level).

I use lagged rather than contemporaneous nonattainment status because (a) state regulations may not take effect in the first nonattainment year (as outlined) and (b) some firm responses plausibly require substantial time to implement (e.g., existing contracts might limit fuel switching). Defining treatment in this way invokes an additional identifying assumption, exogeneity of distance to the nearest nonattainment monitor, which I discuss in section IVC. Because maintenance plans make most SIP regulations permanent, I assign a plant to the treatment group in any year after it is first treated, even if the county in which it is located is redesignated as in attainment of CAA standards.

The rule I employ to estimate threshold distance warrants discussion. There are other possible decision rules—for example, the distance at which the local polynomial first achieves a 0 value or the distance at which the local polynomial takes on a 0 slope, but my choice is conservative in the following sense. Given the findings of Auffhammer et al. (2009) and Bento et al. (2014) and figure 1, I expect that treatment intensity declines with increasing distance to the nearest nonattainment monitor. My rule will tend to estimate a lower threshold distance than many alternative rules. If my rule errs, it does so by assigning treated plants to the control group. In a difference-in-differences design, such misclassifications will bias the magnitudes of my estimates downward. The effect of the selected rule on precision is ambiguous: relative to other rules, it will reduce the heterogeneity of the treatment effect (increasing power), but it will also reduce the number of treated plant-years (decreasing power). In section VIA, I vary the threshold distance and find evidence consistent with these predictions.

### C. Treatment Exogeneity

In equation (3), conditional exogeneity requires 0 correlation between time-varying plant-level unobservables and treatment. More specifically, I assume conditional exogeneity of county-level attainment status and distance to the nearest nonattainment monitor. As for the first assumption, the literature has accumulated substantial evidence that county nonattainment is exogenous.9 Chay and Greenstone (2003a, 2003b, 2005) document that $PM10$ nonattainment counties do not differ systematically from attainment counties on observable dimensions in either levels or changes. Appendix table A4 shows that the emissions profiles of plants in $PM$ attainment and nonattainment counties are not statistically different in my data.

Nonattainment is plausibly exogenous if a given firm produces a small portion of the ambient air pollution in a county. For the average plant in a nonattainment county, this is a tenable assumption. Motor vehicles typically account for the majority of PM pollution, especially in urban areas. The California Air Resources Board estimates that 74% of $PM10$ emissions come from nonpoint sources like road dust and from residential fuel combustion (Auffhammer et al., 2011).

The spatial heterogeneity documented in section IV, however, calls into question the exogeneity of CAA regulation for treated plants. CAA regulations primarily affect plants within 1 kilometer of a nonattainment monitor. It might be that past emissions by a given plant were pivotal in pushing its county above the CAA standard. If that were the case, CAA regulation would be endogenous to past emissions by treated plants. For example, if a plant experienced particularly strong demand for its output in a given year, it might have emitted more air pollution than usual and pushed the nearby monitor above the CAA standard. If output shocks were negatively autocorrelated, my estimates would then overstate the magnitude of CAA effects on air emissions. If instead output shocks were positively autocorrelated, it would understate them.

To investigate the possibility of endogenous entry into treatment, I estimate an event-study specification for air emissions:
$lnAit=αi+δt+∑j=-55τj+ɛit.$
(7)
The variables $τj$ are indicators for a time index defined relative to treatment. A county receives a nonattainment designation in year $τ=-1$ and plants near a nonattainment monitor enter treatment the following year ($τ=0$; “treatment” here refers to the definition given in section IVB). I omit the dummy for the final pretreatment year $τ=-1$, so other coefficients are estimated relative to that year. Figure 2 presents coefficient estimates. If the figure showed higher air emissions at $τ=-1$, that would be evidence of endogenous entry into treatment. While the (normalized) point estimate at $τ=-1$ is indeed greater than those at $τ=-2$ and $τ=-3$, the differences are small and statistically insignificant. Air emissions are roughly flat in the pretreatment period and decline steeply after treatment begins, reaching −50 log points at $τ=4$.10
Figure 2.

Event Study Estimates, On-Site Air Emissions

Estimates from equation (7). Dependent variable is log air emissions (pounds). Reference year is $τ=-1$. A county enters nonattainment in year $τ=-1$, and plants within approximately 1 kilometer of a nonattainment monitor enter treatment in the following year ($τ=0$). The dependent variable is log air emissions. Unit of observation is a plant-year. SEs clustered at the county level.

Figure 2.

Event Study Estimates, On-Site Air Emissions

Estimates from equation (7). Dependent variable is log air emissions (pounds). Reference year is $τ=-1$. A county enters nonattainment in year $τ=-1$, and plants within approximately 1 kilometer of a nonattainment monitor enter treatment in the following year ($τ=0$). The dependent variable is log air emissions. Unit of observation is a plant-year. SEs clustered at the county level.

The second identifying assumption is exogeneity of distance to the nearest nonattainment monitor. Violations of this assumption could spring from two sources: firm location decisions and state monitor placement decisions. Just as firms have incentives to locate in attainment counties (Becker & Henderson, 2000), they may have incentives to enter less monitored areas within a county or monitored areas well below CAA thresholds. If such decisions are a function of time-varying firm unobservables, they may introduce bias.

The state monitor location decision requires more discussion. Importantly in this setting, EPA placement rules largely depend on population characteristics, not firm characteristics. For example, the agency requires monitors in areas of high population density (Bento et al., 2014) and near large, sensitive populations (e.g., asthmatic children; Raffuse et al., 2007). Two types of monitor sites raise potential endogeneity concerns: “sites located to determine the impact of significant sources or source categories on air quality” and “sites located to determine the highest concentrations expected to occur in the area covered by the network” (CFR, 2015).11 The latter type of site is of particular concern given recent work by Grainger et al. (2018), who find that states may strategically locate monitors away from local air pollution maxima. Such behavior could create correlation between time-varying plant unobservables and the distance to the nearest monitor. Note, however, that my identifying assumption is exogeneity of distance to the nearest nonattainment monitor, not distance to the nearest monitor. For strategic location decisions to bias my estimates, states /or plants would have to accurately predict monitor-level violations.

To indirectly evaluate this threat to identification, I regress the log distance to the nearest nonattainment monitor on year fixed effects and the only available time-varying observable: changes in log emissions for untreated plant-years. A negative estimate would be consistent with states strategically placing monitors near faster-growing emissions sources. Table A9 shows that all estimates are 0 to two decimal places and are not statistically significant. Emissions growth rates in untreated plant-years do not predict distance from nonattainment monitors.12

## V. Empirical Results

### A. Cross-Media Substitution, All Industries

Panel A in table 2 presents effects on emissions ratios, based on equation (3), by medium across all industries. The dependent variable is a log emissions ratio, with emissions into a given medium (indicated in the column heading) in the numerator and air emissions in the the denominator. Positive estimates imply positive net elasticities of substitution. There is statistically significant evidence of substitution toward on-site water emissions $β^=1.02$, which include discharges to surface water bodies like rivers and lakes, and offsite water emissions $β^=.58$. As many end-of-pipe abatement technologies recover more than 90% of particulates (World Bank Group, 2017), such substitution is technologically feasible, but recall that this estimate may also reflect other abatement strategies, including process changes and fuel switching. The negative estimates for on-site other and offsite other emissions demonstrate that the ratio approach does not force positive net elasticities of substitution.13 The group of plants identifying the CAA treatment effect differs across columns because not all plants emit into all media. This is important for interpretation of the estimates, but it is not a source of bias unless treatment influences selection into nonnegative emissions. In appendix table A19, I estimate linear probability models and find no evidence that treatment influences such selection. Panel B adds county-year fixed effects, and estimates are essentially unchanged from panel A, except for recycling, which increases substantially $β^=.73$. Panel C adds industry-year fixed effects, and again the estimates are quite similar.

Table 2.
Effect on Log Emissions Ratios, Other Media
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
A. Plant and Year FE
Treated 1.022*** 0.492 −0.373 0.578* 0.262 −0.944 0.119
(0.374) (0.647) (0.608) (0.317) (0.284) (0.593) (0.420)
B. County $×$ Year FE
Treated 1.179*** 0.670 −0.369 0.686** 0.498* −0.525 0.730*
(0.368) (0.612) (0.603) (0.306) (0.284) (0.581) (0.426)
Panel C: County $×$ Year and Industry $×$ Year FE
Treated 1.179*** 0.670 −0.369 0.686** 0.498* −0.525 0.730*
(0.368) (0.613) (0.604) (0.306) (0.284) (0.582) (0.426)
Observations 35,584 17,326 8,067 41,028 59,680 34,435 73,576
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
A. Plant and Year FE
Treated 1.022*** 0.492 −0.373 0.578* 0.262 −0.944 0.119
(0.374) (0.647) (0.608) (0.317) (0.284) (0.593) (0.420)
B. County $×$ Year FE
Treated 1.179*** 0.670 −0.369 0.686** 0.498* −0.525 0.730*
(0.368) (0.612) (0.603) (0.306) (0.284) (0.581) (0.426)
Panel C: County $×$ Year and Industry $×$ Year FE
Treated 1.179*** 0.670 −0.369 0.686** 0.498* −0.525 0.730*
(0.368) (0.613) (0.604) (0.306) (0.284) (0.582) (0.426)
Observations 35,584 17,326 8,067 41,028 59,680 34,435 73,576

Estimates correspond to equation (3). The dependent variable is the log emissions ratio (pounds), with the numerator indicated atop the column and the denominator air emissions in all columns. All specifications include plant fixed effects. The unit of observation is a plant-year. Observation counts differ across columns because not all plants report emissions into all media. “On-site other” emissions include waste piles, leaks, and spills. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

As explained in sections II and IVA, the ratio estimates of table 2 are scalar multiples of underlying net substitution elasticities. Assuming treatment increases the price ratio $pApW$, the estimates and the underlying elasticities have the same sign. By itself, this fact is informative. Note, for example, that table 3 shows decreased gross emissions to offsite water (the two inputs are gross complements). One might erroneously infer that air emissions and offsite water emissions are net complements. In the ratio specification (table 2), however, the estimate is positive and statistically significant, suggesting these two forms of emissions are net substitutes. A similar pattern holds for recycling, which yields negative estimates in the nonratio specifications and positive estimates in the ratio specifications. To obtain the elasticity from one of these ratio estimates, one must divide by the percentage change in relative prices produced by treatment, which is unobserved. Given $β^=1.02$ for on-site water emissions, if the increase in relative prices is less than 102 log points, then $σ>1$. That suggests that in the aggregate U.S. production function, there is a good deal of net substitutability between on-site air pollution and on-site water pollution.

Table 3.
Effect on Log Emissions, Other Media
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
A. Plant and Year FE
Treated 0.719** 0.192 −0.00728 −0.0677 −0.0949 −0.770 −0.153
(0.337) (0.610) (0.682) (0.248) (0.272) (0.528) (0.229)
B. County $×$ Year FE
Treated 0.779* 0.638 −0.370 −0.0343 −0.243 −1.148** −0.116
(0.408) (1.953) (0.306) (0.287) (0.341) (0.578) (0.300)
C. County $×$ Year and Industry $×$ Year FE
Treated 0.718* 0.108 −0.932*** 0.00566 −0.245 −1.164** −0.0627
(0.415) (1.844) (0.357) (0.274) (0.329) (0.586) (0.309)
Observations 39,592 18,989 9,755 51,294 71,048 43,220 91,806
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
A. Plant and Year FE
Treated 0.719** 0.192 −0.00728 −0.0677 −0.0949 −0.770 −0.153
(0.337) (0.610) (0.682) (0.248) (0.272) (0.528) (0.229)
B. County $×$ Year FE
Treated 0.779* 0.638 −0.370 −0.0343 −0.243 −1.148** −0.116
(0.408) (1.953) (0.306) (0.287) (0.341) (0.578) (0.300)
C. County $×$ Year and Industry $×$ Year FE
Treated 0.718* 0.108 −0.932*** 0.00566 −0.245 −1.164** −0.0627
(0.415) (1.844) (0.357) (0.274) (0.329) (0.586) (0.309)
Observations 39,592 18,989 9,755 51,294 71,048 43,220 91,806

Estimates correspond to equation (4). The dependent variable is log emissions (pounds), with the medium indicated atop the column. All specifications include plant fixed effects. The unit of observation is a plant-year. Observation counts differ across columns because not all plants report emissions into all media. Observation counts are weakly larger than in table 2 because ratios are undefined in plant-years with 0 reported air emissions. “On-site other” emissions include waste piles, leaks, and spills. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

In some cases, gross responses, including output effects, may be of interest. Panel A of table 3 shows results from equation (4), adopting log emissions rather than a log emissions ratio as the dependent variable. Treated plants increase on-site water emissions by 105% (72 log points). This is evidence that water and air emissions are gross substitutes in production. The large magnitude of the estimate stems from low baseline water emissions at treated plants (285 pounds). By mass, the water emissions increase (299 pounds) is approximately 9% of the air emissions decrease (3,230 pounds) at treated plants.14 In interpreting this water pollution increase, it may be instructive to compare it with other estimated treatment effects of environmental regulation on production. Gray et al. (2014), for example, find a 3% to 7% decrease in paper-industry labor input as a result of EPA's 2001 Cluster Rule. Greenstone (2002) finds employment reductions of 1% to 2.4% in response to county-level particulate nonattainment, while Curtis (2018) finds reductions of 1.3% to 5% in response to the $NOx$ budget program. Returning to table 3, effects on other media are not statistically significant in panel A. Panel B adds county-year fixed effects and the estimate for water increases slightly, to 78 log points. This estimate is significant at the 10% level. The estimate for “off-site other” becomes more negative and statistically significant at the 5% level, indicating gross complementarity. Panel C adds industry-year fixed effects; the on-site water estimate is 72 log points, significant at the 10% level. The estimate for “on-site other” becomes more negative and statistically significant at the 1% level.

### B. Cross-Media Substitution, by Industry

It is difficult to analyze substitution patterns at the industry level due to the small number of treated plants. Recall that not all plants in nonattainment counties are treated. Moreover, not all plants emit into all media. Nonetheless, to illustrate the heterogeneity in substitution responses, table 4 presents net estimates for selected industries. (Appendix table A20 shows gross effects on log emissions by industry.) Estimates again come from equation (3). Observed responses are generally consistent with feasible abatement technologies described in the World Bank Environmental Health and Safety Guidelines (World Bank Group, 2017). In the discussion that follows, note that in some cases, I cannot reject the null hypothesis of equal coefficients across industries, and so the heterogeneity is merely suggestive.

Table 4.
Effect on Log Emissions Ratios, by Industry
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
Iron and steel 1.656** 0.878*  −0.384 −0.156 −0.721 0.920
(0.689) (0.440)  (0.322) (0.432) (1.818) (0.805)
Observations 1,853 413  745 1703 1,128 1,934
Nonferrous foundries 0.929     1.894*** 1.451***
(0.711)     (0.606) (0.281)
Observations 203     259 582
Petroleum refining 3.432**   0.832 1.860** 0.712 0.338
(1.538)   (1.796) (0.795) (1.486) (1.853)
Observations 1490   413 1,821 1,268 1,722
Fossil electric power 1.930*** 1.533*** −2.204***  1.816 −0.771 −2.429***
(0.652) (0.0850) (0.725)  (1.119) (0.530) (0.197)
Observations 4,775 4,989 1,220  3,581 2,160 1,770
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
Iron and steel 1.656** 0.878*  −0.384 −0.156 −0.721 0.920
(0.689) (0.440)  (0.322) (0.432) (1.818) (0.805)
Observations 1,853 413  745 1703 1,128 1,934
Nonferrous foundries 0.929     1.894*** 1.451***
(0.711)     (0.606) (0.281)
Observations 203     259 582
Petroleum refining 3.432**   0.832 1.860** 0.712 0.338
(1.538)   (1.796) (0.795) (1.486) (1.853)
Observations 1490   413 1,821 1,268 1,722
Fossil electric power 1.930*** 1.533*** −2.204***  1.816 −0.771 −2.429***
(0.652) (0.0850) (0.725)  (1.119) (0.530) (0.197)
Observations 4,775 4,989 1,220  3,581 2,160 1,770

All columns are based on equation (3). The dependent variable is log emissions ratio (pounds), with the numerator indicated atop the column and the denominator air emissions in all columns. All specifications include plant and year fixed effects. The unit of observation is a plant-year. Observation counts differ across columns because not all plants report emissions into all media. “On-site other” emissions include waste piles, leaks, and spills. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

Point estimates for water pollution are large, positive, and statistically significant for iron and steel, petroleum refining, and fossil electric power.15 Iron and steel plants often employ wet scrubbers because of conductivity problems with electrostatic precipitators: “The presence of fine dust, which consists mainly of alkali and lead chlorides, may limit the efficiency of [electrostatic precipitators]” (World Bank Group, 2017). Petroleum refineries may substitute toward water for a different reason: wet scrubbers remove some gaseous pollutants that would otherwise condense to form particulates. In nonferrous foundries, “Dust from emissions control equipment … often contains sufficient levels of metals to make metal recovery economically feasible. Filter dust should be recirculated in the furnaces, to the extent possible. This allows metal recovery through dust reprocessing, and therefore minimizing waste to landfills” (World Bank Group, 2017). Estimates show that such foundries respond to treatment by increasing emissions to recyclers, but they generally do not report emissions to landfills. Iron and steel plants, by contrast, exhibit a smaller and statistically insignificant increase in recycling. In fossil electric power, estimates reveal net substitution not only toward on-site water (193 log points), consistent with wet scrubbing, but also in land disposal: 153 log points on-site and 182 log points off-site (with the latter not statistically significant). These land discharges are consistent with the use of electrostatic precipitators and fabric filters for particulate abatement.

This heterogeneity could be used to target regulatory enforcement. Table 4 suggests that in counties entering CAA nonattainment, a regulator might want to scrutinize more closely: water emissions from metals, petroleum refining, and power plants and land emissions from power plants. Some substitution (e.g., recycling by nonferrous metal plants) is unlikely to reduce social welfare and would not warrant additional scrutiny.

### C. Leakage

Table 5 provides evidence on my intrafirm leakage hypothesis. For the average plant in an attainment county, treatment of one or more plants within the same firm and industry increases air emissions by 11%. The estimate is statistically significant at the 5% level. Column 2 adds county-year fixed effects and the estimate is identical, though statistically significant only at 10%. Column 3 adds industry-year fixed effects; both the point estimate and the standard error are similar. Columns 4 through 6 model exposure to treated plants within the firm using two dummies—the first for exactly one treated plant and the second for two or more treated plants. Estimates imply exposure to one treated plant increases emissions by 10%, while exposure to two or more treated plants increases emissions by approximately 20%. In column 4, estimates are statistically significant at the 10% level, but in columns 5 and 6, estimates are less precise and $t$-statistics are in the 1.5 to 1.6 range. While air emissions leakage need not imply one-for-one increases in output at untreated plants, my estimate is roughly comparable to that of Levinson and Taylor (2008), who find that environmental regulation in a given industry increases net imports of its output by 10%. Similarly Hanna (2010) finds a 9% increase in foreign output of U.S.-based multinationals in response to the CAA Amendments of 1990.

Table 5.
Leakage of Air Emissions, within Firm and Industry
(1) On-Site Air(2) On-Site Air(3) On-Site Air(4) On-Site Air(5) On-Site Air(6) On-Site Air
1$+$ other treated plants 0.110** 0.110* 0.111*
(0.0538) (0.0593) (0.0617)
1 other treated plant    0.101* 0.0901 0.0988
(0.0541) (0.0588) (0.0619)
2$+$ other treated plants    0.200* 0.307** 0.229
(0.117) (0.138) (0.144)
Industry $×$ Year FE No No Yes No No Yes
County $×$ Year FE No Yes Yes No Yes Yes
Year FE Yes No No Yes No No
Plant FE Yes Yes Yes Yes Yes Yes
Observations 128,543 128,543 128,543 128,543 128,543 128,543
(1) On-Site Air(2) On-Site Air(3) On-Site Air(4) On-Site Air(5) On-Site Air(6) On-Site Air
1$+$ other treated plants 0.110** 0.110* 0.111*
(0.0538) (0.0593) (0.0617)
1 other treated plant    0.101* 0.0901 0.0988
(0.0541) (0.0588) (0.0619)
2$+$ other treated plants    0.200* 0.307** 0.229
(0.117) (0.138) (0.144)
Industry $×$ Year FE No No Yes No No Yes
County $×$ Year FE No Yes Yes No Yes Yes
Year FE Yes No No Yes No No
Plant FE Yes Yes Yes Yes Yes Yes
Observations 128,543 128,543 128,543 128,543 128,543 128,543

Estimates correspond to equation (5), where “other treated plant” is a treated plant within the same firm and industry (six-digit NAICS code). The dependent variable is log air emissions (pounds). The unit of observation is a plant-year. The sample is restricted to plants in attainment counties. Parent firm identifiers come from TRI data. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

Interpreting the estimates in table 5 as causal requires that the leakage plants do not differ from other attainment-county plants in time-varying, unobservable ways. Appendix table A5 shows that emissions profiles for leakage and nonleakage plants are not significantly different. I define the boundary of the firm using TRI parent company identifiers. If these identifiers are at a level below the ultimate corporate parent, my estimates will likely understate the true amount of leakage. Likewise, if there is general-equilibrium leakage to plants owned by other firms in attainment counties, my estimates will be biased downward (see appendix E). This model will not capture within-firm leakage to plants located in nonattainment counties but beyond the threshold distance.

The following back-of-the envelope calculation estimates the ratio of leakage to air emissions abatement at the firm level. The average treated firm in my data includes approximately one treated plant and eighteen leakage candidates: plants within the same industry that are located in attainment counties.16 Average air emissions at eventually treated plants prior to treatment are 8,501 pounds, while average baseline emissions at leakage candidates are 667 pounds. The estimate from column 3 of table 5 implies the following net change in emissions from treating an average firm. The firm's treated plant reduces emissions by $.38×8,501=3,230$ pounds.17 The eighteen candidate plants together increase emissions by roughly $18×.1×667≈1,200$ pounds. On net, then, the average firm treated under the CAA decreases particulate air emissions by $3,230-1,200=2,030$ pounds. Roughly 37% of reductions at treated plants are offset by leakage. (While a full welfare analysis is beyond the scope of this paper, appendix E.3 offers a few relevant observations.) This result should be interpreted with several important caveats in mind. First, the TRI data cover only large plants, which may be more likely to belong to multiplant firms and thus may have more scope for within-firm leakage. Second, these estimates describe only TRI-reportable particulate emissions. They do not capture international leakage of the type that Hanna (2010) analyzes. Third, industrial sources account for approximately 25% of particulate emissions in an average county (Auffhammer et al., 2011), so the implied changes in ambient pollution are much smaller than the emissions changes I estimate at the plant level.

Leakage does present a potential problem in using difference-in-differences designs to evaluate the CAA, as it is a spillover from the treatment group (typically nonattainment counties) to the control group (attainment counties). The spillovers identified in table 5 imply that such analyses overstate CAA benefits in nonattainment counties and fail to account for some of the costs in attainment counties. My estimated gross effects on air emissions (appendix table A10) will be biased upward in magnitude, and my estimated gross effects on other emissions (table 3) will be biased downward in magnitude. Such bias may be small, however, if within-firm leakage accounts for a small share of aggregate emissions and ambient pollutant concentrations in attainment counties. Provided the optimal input ratio is independent of scale, spatial leakage will not bias my ratio-based net estimates (table 2).

## VI. Additional Results, Robustness, and Placebos

### A. Distance Threshold

Section IVB discussed the rule used to estimate the threshold distance from a nonattainment monitor and made predictions about alternative distances. Appendix table A15 shows effects on air emissions at five threshold distances, with two smaller and two larger than the 1.07 kilometers used in my primary analyses. As predicted, smaller thresholds increase estimate magnitudes. This is consistent with plants closer to nonattainment monitors being regulated more intensively. Larger thresholds decrease estimate magnitudes, as the models begin to include untreated plants in the treatment group. Appendix table A23 performs a similar exercise for my models of on-site water emissions. While the estimates are less precise, the same broad pattern holds, with lower-magnitude treatment effects as threshold distance increases. Finally, appendix table A26 estimates intrafirm leakage, again varying threshold distance. Again, estimate magnitudes decline with increased threshold distance. In none of these tables is the sign or rough magnitude of my estimate appreciably altered by the choice of threshold. In tables A15 and A26, statistical significance is also unaffected. In table A23, however, some of the alternative thresholds do yield estimates that are not statistically significant. As predicted in section IV, precision is not monotonically related to distance.

Appendix figure A2 demonstrates that the threshold is not sensitive to the range over which one plots the local polynomial. The left panel extends the range of the horizontal axis to 8.5 kilometers (50th percentile) and the right to 53 kilometers (95th percentile). In both cases, the threshold distance is extremely close to the one used in my primary analysis. There is no evidence of a treatment effect on plants beyond the threshold distance.

### B. Cross-Media Substitution

My theoretical model predicts that a plant's input ratio will be independent of output, so cross-media substitution and intrafirm leakage can be analyzed independently. To test this prediction, I estimate my leakage model using an emissions ratio as the dependent variable and report results in appendix table A21. Estimates are generally near 0 and statistically insignificant, with the exceptions of on-site other (42 log points; statistically significant at the 1% level) and off-site land (−28 log points; statistically significant at the 1% level). In my cross-media model (table 3), this leakage will produce a downward bias in the on-site other estimate and an upward bias in the off-site land estimate because of emissions changes in the control group. Such bias is small, however, as leakage candidates constitute a small fraction of control-group plants.

To facilitate comparison with previous literature, appendix table A22 presents estimated effects of county nonattainment on log emissions in levels and first differences. These are small and statistically indistinguishable from 0 in most cases because (a) they average non-0 responses at treated plants with a larger number of 0 responses at untreated plants in nonattainment counties and (b) a first-differenced dependent variable will be near 0 once emissions reach their long-run posttreatment level. Point estimates are similar to the Greenstone (2003) and Gamper-Rabindran (2009) results.

### C. Leakage

Intuitively one would expect leakage to be more feasible when plants are technologically similar. As a robustness check on my leakage results, I estimate the same model, grouping plants by firm and a coarser industry classification (four-digit NAICS code). Results are in appendix table A24. Consistent with intuition, estimates are roughly half the magnitude of those from my preferred specification and not statistically significant. One might also expect proportionally smaller leakage effects in larger firms, where there are more plants available to absorb a given output increase. In appendix table A25, I estimate leakage models in which treatment interacts with firm size. Estimated interaction effects are very small, and their signs vary. This pattern is inconsistent with the hypothesis regarding firm size, which predicts negative interaction effects.

### D. Placebos

Treatment should have no direct effect on plants that do not emit any air pollution. Table 6 tests this hypothesized null effect by estimating a variant of equation (4), where treatment is interacted with a dummy indicating 0 air emissions. If my model is well specified, it should find no effect of CAA regulation on these plants. The estimates are not statistically significant. Importantly the estimated effect on on-site water emissions from plants without air emissions is near 0. This suggests the estimated increase in on-site water emissions in table 3 does not arise from gross misspecification.

Table 6.
Placebo Effect on Log Emissions
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
Treated $×$ No Air Emissions 0.0758 0.142 0.546 −0.415 −0.944 −1.175 −0.381
(0.210) (0.428) (0.667) (0.426) (0.646) (0.828) (0.304)
Treated $×$ Air Emissions 0.790** 0.202 −0.361 0.0909 0.0667 −0.615 −0.0990
(0.349) (0.639) (0.632) (0.214) (0.233) (0.496) (0.233)
Year FE Yes Yes Yes Yes Yes Yes Yes
Plant FE Yes Yes Yes Yes Yes Yes Yes
Observations 41,520 20,100 10,773 61,449 82,066 51,509 117,844
(1) On-Site Water(2) On-Site Land(3) On-Site Other(4) Off-Site Water(5) Off-Site Land(6) Off-Site Other(7) Recycled or Treated
Treated $×$ No Air Emissions 0.0758 0.142 0.546 −0.415 −0.944 −1.175 −0.381
(0.210) (0.428) (0.667) (0.426) (0.646) (0.828) (0.304)
Treated $×$ Air Emissions 0.790** 0.202 −0.361 0.0909 0.0667 −0.615 −0.0990
(0.349) (0.639) (0.632) (0.214) (0.233) (0.496) (0.233)
Year FE Yes Yes Yes Yes Yes Yes Yes
Plant FE Yes Yes Yes Yes Yes Yes Yes
Observations 41,520 20,100 10,773 61,449 82,066 51,509 117,844

Estimates correspond to equation (4), but estimates for “Treated$×$No Air Emissions” report the effect of placebo treatment (being near a nonattainment monitor) on plants with no air emissions, which should not be affected by the CAA. Estimates for “Treated$×$Air Emissions” are for actually treated plants; they are not placebos. The medium is indicated atop the column. All specifications include plant and year fixed effects. The unit of observation is a plant-year. Observation counts differ across columns because not all plants report emissions into all media. Observation counts are weakly greater than in table 3 because placebo plants are included. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

Table 7 reports results from a placebo test of my leakage model. I construct variables based on placebo “treated” plants: plants within the same firm and industry that are located in nonattainment counties but farther than 8 kilometers from the nearest nonattainment monitor. As these plants are not treated, one should not see increased air emissions by attainment-county plants in the same firm and industry. If my leakage model is capturing, for example, changes in the geographic distribution of output that happen to be correlated with treatment, this placebo test should return large, positive estimates. Instead, the estimates in table 7 are in the range from −5% to 1% and are not statistically significant. This suggests that the leakage results in table 5 do not spring from an omitted variable problem.

Table 7.
Placebo Leakage Effect, within Firm and Industry
(1) On-Site Air(2) On-Site Air(3) On-Site Air(4) On-Site Air(5) On-Site Air(6) On-Site Air
1+ other placebo plants 0.00467 −0.00396 −0.0257
(0.0298) (0.0335) (0.0333)
1 other placebo plant    −0.000401 −0.00325 −0.0142
(0.0346) (0.0382) (0.0381)
2+ other placebo plants    0.0126 −0.00512 −0.0461
(0.0367) (0.0421) (0.0417)
Industry $×$ Year FE No No Yes No No Yes
County $×$ Year FE No Yes Yes No Yes Yes
Year FE Yes No No Yes No No
Plant FE Yes Yes Yes Yes Yes Yes
Observations 128,543 128,543 128,543 128,543 128,543 128,543
(1) On-Site Air(2) On-Site Air(3) On-Site Air(4) On-Site Air(5) On-Site Air(6) On-Site Air
1+ other placebo plants 0.00467 −0.00396 −0.0257
(0.0298) (0.0335) (0.0333)
1 other placebo plant    −0.000401 −0.00325 −0.0142
(0.0346) (0.0382) (0.0381)
2+ other placebo plants    0.0126 −0.00512 −0.0461
(0.0367) (0.0421) (0.0417)
Industry $×$ Year FE No No Yes No No Yes
County $×$ Year FE No Yes Yes No Yes Yes
Year FE Yes No No Yes No No
Plant FE Yes Yes Yes Yes Yes Yes
Observations 128,543 128,543 128,543 128,543 128,543 128,543

Estimates correspond to equation (5), but using variables based on placebo-treated plants: plants are within the same firm and industry (six-digit NAICS code), located in nonattainment counties, but farther than 8 kilometers from the nearest nonattainment monitor. The dependent variable is log air emissions (pounds). The unit of observation is a plant-year. The sample is restricted to plants in attainment counties. Parent firm identifiers come from TRI data. SEs are clustered at the county level. ***$p<0.01$, **$p<0.05$, and *$p<0.1$.

## VII. Conclusion

While economists have long recognized the potential for substitution responses to location-specific, single-medium pollution regulation, empirical studies have found little evidence of cross-media effects. Using specifications motivated by classical firm optimization theory, this study provides evidence of regulation-induced pollution substitution in response to the Clean Air Act. Estimates from EPA Toxic Release Inventory data show that CAA-regulated plants increase their ratio of water to air emissions by 177% (102 log points) and their level of water emissions by 105% (72 log points). This response offsets 9% of air emissions reductions. Particulate regulation of an average plant increases air emissions at unregulated plants owned by the same firm by 11%. At the firm level, such leakage offsets 37% of emissions reductions. This paper, moreover, examines only two possible types of pollution substitution. New source performance standards mean that new plants may use nonair pollution inputs more intensively and locate more frequently in attainment counties (the latter is documented in Henderson, 1996, and Becker & Henderson, 2000). Thus, industry- or economy-wide responses may be larger in magnitude than the plant- and firm-level responses identified in this study.

A policy with efficiency among its goals should account for these firm responses. A maximally efficient policy, with emissions into every medium and location priced according to marginal damage, would be difficult to design and costly to administer. Moreover the primary goal of the Clean Air Act is not efficiency but safeguarding human health (U.S. EPA, 2011). Given any set of goals, however, it is easier to formulate effective policy when policymakers have well-identified estimates of firm responses. For example, my cross-media results suggest that restricting water emissions or increasing water quality monitoring in CAA nonattainment counties might be important for protecting public health. They also suggest EPA's recent proposed changes in water rules may meaningfully alter firm emissions decisions. My estimates of within-firm particulate leakage suggest that leakage could pose a first-order problem for the state and regional greenhouse gas regulations currently attracting policy interest in the United States.

I also document spatial heterogeneity in regulatory intensity. Most plants in nonattainment counties show no evidence of being regulated, but plants near nonattainment monitors show large air emissions decreases. This pattern is consistent with theoretical models in which regulators seek to minimize costs (political or pecuniary) in implementing the CAA, but there are other possible explanations. Questions concerning state implementation of federal environmental regulations warrant additional research, building on work like Helland (1998a), Levinson (2003), and Sigman (2003, 2005). Legislators might also want to consider the regulator behavior implied by my spatial heterogeneity result when designing future policy.

The welfare effects of regulation-induced pollution substitution present an interesting subject for future research. Air pollution regulations can have large benefits (Chay & Greenstone, 2003b; Currie & Neidell, 2005). In particular, EPA estimated the 1970–1990 benefits of the Clean Air Act (CAA) at \$22 trillion (U.S. EPA, 2011). While social costs from firm reoptimization are plausibly smaller than the benefits of the CAA, they may be large in absolute terms and have important distributional consequences.

## Notes

1

I define a nonattainment monitor as one that exceeds the CAA standards for $PM10$ or $PM2.5$. Additional discussion is in section IVB.

2

This is equivalent to assuming that plant-level production functions are homothetic (Shephard, 1953).

3

Above, CRS would imply $fQ=Q$. CRS is not necessary for optimal input ratios to be independent of scale. Intuitively, if changes in $Q$ produce proportional changes in the marginal products of $W$ and $A$, then $W*A*$ is independent of $Q$ even if returns to scale are not constant (Leontief, 1947). Functional forms like CES and Cobb-Douglas, commonly used to model production, exhibit multiplicative separability irrespective of returns to scale.

4

This prediction is admittedly trivial in a two-plant model with $Q$ held fixed. In practice $Q$ may vary, and I test empirically for leakage in section VC.

5

Michael Greenstone (2003) generously shared his mapping from TRI chemicals to CAA criteria pollutants. EPA regulates $PM10$ (particles <10 microns in diameter) and $PM2.5$ (<2.5 microns in diameter) separately, but the Greenstone data do not allow me to separately identify these categories.

6

An alternative version of scenario a) would involve accurate reporting in the pretreatment period and differential overreporting of water emissions in the posttreatment period. Given the risk of additional regulation or penalties, it is not likely that a plant would respond to increased regulatory scrutiny by increasing its overreporting.

7

As of this writing, 2007–2015 were the only years for which such linked data were available. For additional information on the TRI-DMR merge process, see appendix C.2.

8

Specifications with county-year fixed effects already involve tens of thousands of parameters. In order to avoid the panel measurement error issues discussed in Griliches and Hausman (1986), these industry-year fixed effects employ three-digit NAICS codes.

9

Examples include Henderson (1996), Becker and Henderson (2000), Greenstone (2002), and Auffhammer, Bento, and Lowe (2011).

10

Appendix figure A3 shows similar event study estimates from a specification with county-year and industry-year fixed effects.

11

For more details on monitor placement rules, see appendix B.3.

12

Appendix table A8 presents a version of this specification using emissions levels instead of growth rates. Estimates are practically large and statistically significant. Like figure A4, they imply that plant fixed effects are necessary to recover unbiased estimates.

13

“On-site other” emissions include waste piles, leaks, and spills.

14

Average air emissions in untreated plant-years are 8,501 pounds. The effect of CAA treatment is a decrease of $.38×8,501=3,230$ pounds. Average water emissions in untreated plant-years are 285 pounds. The effect of CAA treatment is an increase of $1.05×285=299$ pounds. In relative terms, $2993230=.09$.

15

For many industries examined in this paper, including nonferrous foundries, proportional increases in emissions into other media are much larger than decreases in air emissions. This is because baseline air emissions are generally much larger than baseline emissions into other media. For example, appendix table A4 shows air emissions are roughly six times greater than water emissions in both attainment and nonattainment counties.

16

This is the mean number of leakage candidates over all treated firms, including single-plant firms that have 0 leakage candidates by definition. The distribution of leakage candidates is highly right skewed, with a median of 7.

17

The 38% reduction is the percentage change corresponding to the estimated treatment effect on log air emissions: $e-.485-1=.38$.

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## Author notes

I thank Quamrul Ashraf, Maximilian Auffhammer, Peter Berck, Prashant Bharadwaj, Richard Carson, Andrew Chamberlain, Julie Cullen, Olivier Deschenes, David Evans, Meredith Fowlie, Joshua Graff Zivin, Michael Greenstone, Carolyn Hayek, Kelsey Jack, Mark Jacobsen, Daniel Karney, David Keiser, Sara LaLumia, Arik Levinson, Matthew Neidell, Jeffrey Perloff, Lynn Russell, Jeremy Schreifels, Ron Shadbegian, Joseph Shapiro, Jeffrey Shrader, Larry Sorrels, Junjie Zhang, and participants in the UC San Diego environmental seminar for invaluable assistance with this project.

A supplemental appendix is available online at http://www.mitpressjournals.org/doi/suppl/10.1162/rest_a_00797.