First Draft Not for Citation or Quotation

Air Pollution and Human Health: An Update*

Michael Greenstone University of Chicago, American Bar Foundation, and NBER

May 2002 *This paper was prepared for the 2nd World Congress of Environmental Economists on the 50th Anniversary of the founding of Resources for the Future. This paper would not have been possible without my collaboration with Kenneth Chay on a series of papers on the health impacts of airborne particulates pollution. This paper discusses some of the results from our papers, but even more importantly our collaboration has sharpened my thinking about empirical work and has directly influenced the ideas contained in the paper. V. Kerry Smith has provided insightful comments and been very patient with my inability to meet any of the deadlines that he has set. I have also benefited greatly from discussions with Jonathan Guryan and James Heckman. Anand Dash deserves special thanks for superb research assistance. The generous financial support of the U.S. Environment Protection Agency and the Hewlett Foundation is gratefully acknowledged.

Most economists associate the birth of the field of environmental economics with the

establishment of Resources for the Future (RFF) fifty years ago in 1952. The coincidence of this

anniversary and the 2nd World Congress of Environmental Economists provide an appropriate

moment to take stock of our field and RFF’s contribution to its development. As part of this

moment of reflection, I have been asked to discuss the state of knowledge on whether there is a

relationship between air pollution and human health and to identify future directions for research

in this area.

A skeptic might initially wonder why this seemingly simple relationship qualifies as an

entire subfield of environmental economics. The answer is that air pollution affects two aspects

of our lives that we hold very dear. On the one hand, it is thought that current air pollution

concentrations harm human health by causing premature mortality and increased rates of

morbidity. Consequently, there is often great support for interventions into the marketplace

aimed at reducing air pollution.

On the other hand, it is widely believed that air pollution is inextricably linked to

economic progress. The right to emit pollution lowers firms’ production costs, allowing them to

expand output, hire more workers, and increase profits. Thus, any policies aimed at reducing

emissions usually face considerable opposition, particularly from those whose profits or jobs

would be directly affected.

The basic problem is that it is almost impossible to be against either advances in human

health or material well being. Who would argue that children should be exposed to air pollution

that causes their premature death? And, who would argue that individuals should not be allowed

to work in the industries in which they can best provide for their material well being? Of course,

the tension between these goals arises because environmental regulations that are believed to

improve human health are also believed to hamper economic progress.

As is usual, this tension is generated by the scarce set of resources available to meet our

multiple desires. This can best be understood by viewing the lost economic activity associated

with reduced air pollution emissions as the cost of clear air. In this framework, clean air is just

another consumer good and it must be evaluated by the utility it provides. One benefit of clean

air is that most people find it more pleasant to live in areas with low levels of air pollution. But,

if it is the case that cleaner air improves health outcomes, thereby allowing more people to make

productive contributions to society, then the benefits of clean air may far exceed its aesthetic

value.

Society’s goal should be to find the level of air pollution that balances the benefits that

emitters receive from polluting against the costs incurred by society as a result of the pollution.

The identification of this optimal level of pollution requires precise estimates of the marginal

benefits and costs associated with each additional unit of pollution. Consequently, reliable

estimates of the relationship between air pollution and human health are of great practical

importance.

In recent years, the value of efforts to reduce air pollution concentrations has become a

source of considerable controversy. Writing about the health effects of tropospheric ozone,

Christopher DeMuth and Randall Lutter state, “Indeed, the effects of the air pollution [ozone] in

question on health are highly uncertain or exceedingly small” (The Weekly Standard 1999). In

contrast, Rob McConnell of the University of Southern California says that recent research

suggests that, “contrary to conventional wisdom, ozone is involved in the causation of asthma”

(Washington Post 2002). Such controversy about the health effects of ozone and other forms of

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air pollution suggests that a review of the evidence on the link between air pollution and human

health and exposition of fruitful directions for future research may be of more than academic

interest at this time.

The starting point for any discussion of what is known about this relationship is the

seminal and exhaustive work of Lester Lave and Eugene Seskin. This work was published in

their 1970 article in Science and 1977 book, both of which are titled Air Pollution and Human

Health. Notably, their research would not have been possible without an initial grant in 1967 and

two subsequent grants-- all from Resources for the Future.1 Their pathbreaking research set the

stage for hundreds of papers that have explored whether air pollution and human health are

causally related. In fact, the Science article has been cited 175 times!

Notably, almost all of this subsequent research can be viewed as a simple fitting of the

statistical models advocated by Lave and Seskin to new data sets. I will show that these

statistical models are likely to be misspecified due to omitted variables, measurement error, or

both. This is because other determinants of human health are different in areas with high

concentrations of air pollution than in areas with low pollution concentrations. Further, it is not

possible to accurately measure individual’s lifetime pollution exposure.

In light of the importance of this relationship, it is crucial to develop new techniques that

build upon Lave and Seskin’s foundation. The ideal solution to this problem of inference is to

run a classical experiment. Of course, such experiments are not ethical in the case of air

pollution. In this paper, I argue that the application of quasi-experimental evaluation techniques

are a fruitful direction for research on the relationship between human health and air pollution.

1 Thus, just as it has done in many other subfields of environmental economics, RFF has played a crucial role in developing the current body of knowledge on the health effects of air pollution.

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In a quasi-experimental evaluation, the researcher exploits differences in outcomes

between a treatment group and a control group, just as in a classical experiment. In the case of a

natural experiment, however, treatment status is determined by nature, politics, an accident, or

some other action beyond the researcher’s control. Despite the “nonrandom” nature of the

treatment status, it is still possible to draw valid inferences from the differences in outcomes

between the treatment and control groups in a natural experiment, provided certain (potentially

testable) assumptions are met. Although it is by no means a requirement, these studies

frequently involve the collection of new data sets or the use of less well known ones. This

research approach has been used extensively in recent years and has permitted more credible

inferences about the impacts of a wide range of public policies (see Angrist and Krueger JEP and

Meyer 1994 for a review). My hope is that this paper will lead to further application of this

research approach in the area of air pollution and human health but also in environmental

economics more generally.

The remainder of this paper is organized as follows. The next section reviews Lave and

Seskin’s Approach and outlines some of the statistical pitfalls associated with it. The third

section produces some estimates of the relationship between human health and air pollution

through the application of the epidemiological approach advocated by Lave and Seskin. Section

IV describes the quasi-experimental approach, highlights some of its pitfalls, and provides some

general advice on how to avoid the pitfalls. Section V describes two recent applications of the

quasi-experimental approach to the question of air pollution and human health and Section VI

concludes.

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II. Review of Lave and Seskin’s Approach

Lave and Seskin’s original article was published in Science in 1970 and the book that this

talk is meant to celebrate was published not long after in 1977. At the time of these publications,

I was 2 years old and 9 years old! When I was asked to put together this talk, my initial thought

was that their work was likely to be important in the context of the seemingly long ago period

that it was written but not terribly impressive by modern standards. A careful read of the book

has demonstrated the truth of the old adage that you cannot judge a book by its cover.

Their book is a wonderful example of how to conduct credible research on air pollution

and human health but, perhaps more importantly, it is an impressive application of the method

that observers have used to develop explanations for the “curious happenings” that are observed

in the real world. That is, it adheres to the Scientific Method that begins with a hypothesis that is

empirically tested and then based on the results of this test the hypothesis is modified and tested

again in an iterative process. Its simplicity makes this method almost banal, and this banality can

obfuscate the fact the Scientific Method deserves much of the credit for what we understand

about the world today in areas as diverse as astronomy, medicine, and even economics.

It is my opinion that it is our duty as researchers to continually ask whether our research

efforts serve this master. And, I think their book is an important reminder for all economists,

environmental and otherwise, and for that matter all researchers that attempt to develop theories

that have predictive power about the “curious happenings” in the world. In this section, I review

Lave and Seskin’s approach to exploring whether there is a relationship between “Air Pollution

and Human Health” in order to highlight their devotion to this approach and to underscore their

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deviations from it. Unfortunately due to space constraints, this review will of necessity be

shorter than the quality of the book merits.

A. Causal Hypotheses and the Fundamental Problem of Causal Inference

Although it may seem obvious, I find it worthwhile to remind myself what constitutes a

causal hypothesis. The definition I like requires a causal hypothesis to contain a manipulable

“treatment” that can be applied to a “subject” and an “outcome” that may or may not respond to

the treatment. A test of a causal hypothesis requires that all other determinants of the outcome

can be held constant in order to isolate the effect of the treatment.2

In the ideal, we would be able to observe the same “subject” in the state of the world

where it received the treatment and the state of the world where it did not receive the treatment.

The disappointing reality is that it is impossible to observe the same subject in both states of the

world. For example in drug trials, we cannot give the new drug and withhold the new drug from

the same person at the same time. This difficulty has been called the “Fundamental Problem of

Causal Inference” and has been recognized since at least Hume (Holland 1986). Consequently,

as Lave and Seskin themselves note, “A causal relationship exists only as a theoretical construct,

not as a set of empirically verifiable propositions” (p. 13).

In practice, the task is to come as close as possible to attaining the unattainable but all the

while remaining cognizant of the necessary assumptions. Returning to the example of new drug 2 This definition of causality is certainly not original. Philosophers as far back as the first half of the 19th century have used similar definitions. For example, John Stuart Mill (1843) wrote: “If an instance in which the phenomenon under investigation occurs, and an instance in which it does not occur, have every circumstance in common save one, that one occurring in the former; the circumstances in which alone the two instances differ, is the effect, or the cause, or an indispensable part of the cause of the phenomenon.” [taken from Holland 1986, p. 951]

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trials, this is why it is necessary to form a control group and give them a placebo. The

empirically unverifiable hope is that the control group serves as a valid counterfactual for what

would have happened to the treated group in the absence of the supply of the new drug. In the

standard framework, the treated and control groups are compared along observable dimensions

in the hope that these variables are balanced across the two groups. If this is the case, then it is

assumed that the treatment is assigned independent of the characteristics of the recipients but, of

course, even in a randomized experiment one can never verify this about the unobservables.

This is why empirical research of causal questions inevitably boils down to an effort to obtain a

valid counterfactual.

Lave and Seskin’s approach can be viewed as an application of the Scientific Method.

Their Chapter 2, titled “Theory and Method”, begins with a clear statement of their hypothesis:

“The central question of our study is, Does air pollution cause increased mortality?” (p. 13). In

the context of the above discussion, their question is a causal one and contains an implicit

hypothesis where air pollution is the treatment, the subjects are humans, and the outcome is

death.

Importantly, their hypothesis also meets Karl Popper’s definition of a scientific theory.

Popper distinguishes between scientific theories and pseudo-scientific theories. The difference is

a simple one. According to Popper, “the criterion of the scientific status of a theory is its

falsifiability, or refutability, or testability” (Popper 1963). Thus, in this framework, a theory can

never be proved to be true but rather only refuted and that through the iterative process of testing

and rejecting theories, it may be possible to develop a nuanced theory that cannot be refuted.

Since it may be that air pollution, at least at moderate levels, does not affect mortality, Lave and

Seskin’s hypothesis can be falsified.

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B. The Rationale for an Epidemiological Approach

Lave and Seskin’s Chapter 2 provides a sophisticated discussion of the difficulties that

underlie efforts to test whether there is a relationship between air pollution and mortality. They

begin by noting that previous researchers had documented an association between these

variables. Given this association, four possibilities exist: (1) the association is due to sampling

variation; (2) air pollution causes mortality; (3) mortality causes air pollution, (4) there is a set of

factors that causes both air pollution and increased mortality. If the last possibility is the source

of the association, then it is due to a spurious correlation.

In general, the solution to this problem of inference is to perform an experiment.

However, Lave and Seskin convincingly argue that in the case of air pollution and human health,

there are at least three reasons that laboratory experiments are impractical. First, it is unethical to

expose people to high levels of air pollution when the hypothesis is that this may harm them.

Second, laboratory experiments are not equipped for detecting long-term, low-level effects. For

example, it is not feasible to quarantine either the treatment or control group for decades in order

to find out if there are health effects. Third, the hypothesized effect may be so small that a

laboratory experiment would require tens of thousands of participants.

Lave and Seskin conclude, “we are left with an epidemiological approach to investigating

the effect of air pollution on mortality. The basic task becomes one of making inferences from

observational (nonexperimental) data” (p. 14).3 Lave and Seskin’s aim is to test whether the

3 Lave and Seskin note that one shortcoming of the epidemiological approach is that it is unable to convincingly explore the pathophysiological mechanism that might underlie a relationship

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association between air pollution and mortality is robust; that is, does it remain when it is tested

in a number of different settings. They write, “We will be looking for a consistent association

between air pollution and mortality in each setting and seeking to ‘eliminate inadequate models’”

(p. 21). Thus, their goal is to rule out that the association is due to unobserved factors.

C. The Epidemiological Approach

Lave and Seskin’s clarity about their hypothesis is matched by their carefulness in

expositing the potential sources of misspecification in the estimation of the relationship between

air pollution and human health. In order to fix thoughts about their approach, it is instructive to

consider the following cross-sectional model, which is similar to the one that they estimate:

(1) yct = Xct′β + θΤct + εct, εct = αc + uct,

(2) Tct = Xct′Π + ηct, ηct = λc + vct,

where yct is some measure of health status (e.g., the mortality rate) in county c in year t, Xct is a

vector of observed determinants of y, and Tt is a summary measure of pollution in the county. εct

and ηct are the unobservable determinants of infant mortality rates and air pollution levels,

respectively, and they are comprised of fixed and transitory components. The coefficient θ is the

‘true’ effect of air pollution on infant mortality.

For consistent estimation, the least squares estimator of θ requires E[εctηct] = 0. If there

are omitted permanent (αc and λc) or transitory (uct and vct) factors that covary with both TSPs

and infant mortality, then the cross-sectional estimator will be biased. It is important to highlight

that equation (1) assumes a particular functional form for the explanatory variables. However, between the air pollution and human health. They argue that a laboratory based experiment is essential for understanding the physiological mechanisms.

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the true functional form is unknown and thus incorrect specification of the functional form may

be a source of misspecification.

One source of omitted variables bias emphasized by Lave and Seskin is that air pollution

may cause individuals who are susceptible to its influences to engage in unobserved (tot he

econometrician) compensatory behavior to mitigate its impact on their health. For example,

people with respiratory diseases might migrate from polluted to clean areas to avoid the health

effects of air pollution. Such migration will bias the estimates downward and could even

produce a “perverse” estimate (i.e., that pollution is associated with a lower incidence of

respiratory-related mortality because the only people living in heavily polluted areas are those

that are immune to its effects).

A related possibility is that susceptible individuals move within a city to less-polluted

neighborhoods or install filters (or other devices) in their homes that clean the air they breathe.

If these compensatory behaviors are more frequent in relatively polluted cities, then they will

also bias the estimates downward. The basic problem is that it is in people’s interests to protect

themselves against pollution, but these efforts undermine our ability to obtain reliable estimates

of the effects of pollution on health.

Lave and Seskin also discuss the possibility that there are other omitted variables that

might bias the estimated association of mortality with air pollution. They write: “We find little

reason to believe that sex distribution, genetic factors, nutrition, smoking, exercise habits, or

medical care are highly correlated with air pollution” (p. 22). My read of this quote is that Lave

and Seskin think a pre-requisite for an unobserved factor to be a source of misspecification is

that there be an economic story for why the factor differs in clean and dirty areas.

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I am much less sanguine, perhaps to the point of being paranoid, that there are other

important differences of the determinants of health that differ in relatively polluted and

unpolluted areas. This unease is partially because I think it is difficult to be clever enough to

think of all the potential economics stories that might cause unwanted correlations. Further in

the relatively small samples that are common for these studies, there are likely to be differences

across sites simply due to random chance. Later, I will present evidence that in fact a wide range

of variables, including per capita income and medical care usage, covary with pollution

concentrations in the cross-section.

Lave and Seskin also highlight that the data sources on pollution introduce two potential

sources of bias. First, it is generally impossible to construct measures of individuals’ lifetime

exposure to air pollution. This is problematical if human health is a function of the population’s

cumulative exposure to pollution. Since historical data on individual’s exposure to pollution is

generally impossible to obtain, Lave and Seskin, as well as scores of subsequent studies on adult

mortality, rely on the assumption that the current measures of air pollution characterize the past

levels.

A simple example highlights the problems with this assumption. Consider the case of

two 30 year-old women living in St. Louis. Suppose that the first woman has lived there her

entire life. The “lifetime exposure” assumption implies that pollution concentrations have been

constant in St. Louis over the last 30 years. Suppose the second woman moved to St. Louis at

age 29. In her case, the assumption implies that the unknown location(s) where she previously

lived had the same pollution levels that St. Louis currently does. Given the dramatic changes in

pollution levels that have occurred both within and across cities over the last 50 years, this

assumption is unlikely to hold for either person.

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The available pollution data introduce a second bias. In particular, most cities have only

a few pollution monitors and the readings from these monitors are used to develop measures of

individuals true exposure to air pollution. Since there is frequently great variation within cities

in pollution concentrations and individuals spend varying amounts of time inside and outside, it

is likely that there is substantial measurement error in the measures of pollution concentrations.

In general measurement error attenuates the estimated coefficient in regressions and the degree

of attenuation is positively related to the fraction of total variation in observed pollution that is

due to mismeasurement.

A frequent suggestion for dealing with omitted variables problems is to use a fixed

effects model that removes all permanent determinants of mortality as potential sources of bias.

However, the costs of this approach can be quite steep because fixed effects can greatly

exacerbate the attenuation bias. This is because in the fixed effects case, the magnitude of the

attenuation bias also depends on the correlation across years in the “true” measures of air

pollution. In order to see this, consider the simplest case, where a measure of air pollution is the

only explanatory variable in a first-differenced linear regression of the form:

(3) yct - yct-1 = θ(Tct - Tct-1) + (uct - uct-1),

where t indicates a particular year and t-1 the previous year. Let the observed air pollution, T,

equal the true value, T*, plus a white noise measurement error so that T = T* + ν, where T* ~

N(0, σ2T*) and ν~ N(0, σ2 ν). It can be derived that: plim θFirst-Difference = θ - θ [σ2

ν /(1 – ρT)( σ2T*

+ σ2 ν)], where ρT = cov(T*t, T*t - 1)/var(T*). The formula indicates that a high correlation in the

“true” year to year values of air pollution greatly exacerbates the attenuation bias. It is

reasonable to assume a county's true air pollution concentrations are highly correlated across

years.

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A common application of the fixed effects approach is to collect data from a single city

and estimate the effect of daily air pollution concentrations on daily health outcomes, typically

mortality.4 In fact, Lave and Seskin estimated these models. These studies rely on the

reasonable presumption that confounding is less likely than in cross-sectional studies since many

of the potential confounding variables (e.g., cigarette smoking patterns, access to medical care,

etc.) are constant within a city over short periods of time. A substantive criticism of these

studies, particularly the ones that focus on mortality as the outcome of interest, is that air

pollution may have caused individuals who were already very ill to die slightly earlier than they

would have otherwise, and that the life expectancy loss is minimal.5 This hypothesis suggests

that the individuals who constituted the “excess” deaths were likely to die in a few days anyway.

Spix, et al. (1994) and Lipfert and Wyzga (1995) find that daily mortality rates declined on the

days immediately following the high pollution days. Consequently, this version of the fixed

effects models may be incapable of identifying long-run health effects.

It is evident that the there are a number of difficulties associated with the epidemiological

approach advocated by Lave and Seskin. These include systematic biases associated with

unmeasured compensatory behavior induced by pollution to standard unmeasured variables to

the mismeasurement of individuals’ lifetime and current exposure to air pollution. Further, one

frequent solution to these problems of misspecification may not be able to identify changes in

human health that are associated with substantial changes in life expectancy. As Lave and

Seskin write, “Needless to say, the estimated parameters are to be viewed with caution” (p. 25).

4 See Dockery and Pope (1996) for a review of these studies. 5 Epidemiologists refer to this phenomenon as “harvesting,” while statistically it is referred to as negative serial correlation.

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D. Is Air Pollution Correlated with the Determinants of Infant Mortality?

The previous subsection highlighted that if measured air pollution is orthogonal to all

predictors of infant mortality, then it is simple to make causal inferences on this relationship. In

this subsection, I examine whether county-level TSPs measures are orthogonal to the observable

predictors of infant mortality, a particularly important measure of human health. It seems

reasonable to presume that if this is the case, then linear regression of infant mortality on TSPs

may suffer from smaller omitted variables bias. For example, if the observable covariates are

balanced, it may be more likely that the unobservables are balanced (Altonji, Elder, and Taber

2000). Second, if TSPs does not covary with the observables, then consistent inference does not

depend on functional form assumptions on the relations between the observable confounders and

infant mortality. Estimators that misspecify these functional forms (e.g., linear regression

adjustment when the conditional expectations function is nonlinear) will be biased.

Table 1 shows the association of 1971 TSPs level with other potential correlates of infant

mortality. The sample is 501 counties that have adequate TSPs monitoring. These counties

account for approximately 60% of all births in the U.S. Column 1 reports the weighted mean of

the determinants of infant mortality (where the weight is the total number of births) in the set of

counties with 1971 TSPs concentrations below the 1971 median. Column (2) reports the

weighted means for the counties with concentrations above the median. Column (3) reports the

p-value from a test that the means in the two columns are equal. If TSPs levels were randomly

assigned across counties, one would expect very few significant differences.

The first column demonstrates that the infant mortality rate is higher in the dirtier

counties, suggesting evidence of an association when the data is unadjusted. However, it is also

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evident other determinants of infant mortality differ across the two sets of counties. The panel

on county-level economic variables indicates that the “dirtier” counties are better off

economically as per-capita income and the employment to population ratio is substantially higher

in these counties. The higher levels of assistance payments imply that the incidence of poverty is

greater in these counties as well.

An examination of the other rows shows that there are significant differences across the

groups for several other key variables, including mother’s race, marital status, prenatal care

usage, age, and history of a previous fetal death. A particularly interesting finding is that the

difference in the percentage of births that are twins is significant at the 10% level. Since the

incidence of the birth of twins is generally considered random, particularly in this period when

fertility drugs were not readily available, this finding underscores the pitfalls of using a cross-

sectional analysis to make inference on the relationship between TSPs and infant health.

Overall, the Column 1 entries suggest that “conventional” cross-sectional estimates may be

biased due to omitted variables or incorrect specification of the functional form of these

important covariates.

It is possible to perform a similar analysis for the changes in TSPs. The idea is to

compare whether changes in observable determinants of infant mortality covary with changes in

TSPs. I do not present the results here, but such an analysis indicates that this generally

decreases the magnitude of the differences across the two sets of counties. However, important

differences remain (e.g., in income and the percentage of mothers with a prior fetal death). As I

discussed above, first differencing the data is also likely to exacerbate the attenuation associated

with measurement error of the TSPs variable. Thus, fixed effects models may also lead to biased

inference.

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III. Estimates from the Traditional Regression/Epidemiological Approach

The last section outlined the traditional epidemiological approach outlined by Lave and

Seskin and highlighted some of its potential shortcomings. Further, it demonstrated that TSPs air

pollution is not orthogonal to important observable determinants of infant mortality in either

levels or changes.

Here, I implement the traditional epidemiological approach. Rather than recycle their

results, I have chosen to do this with data that I collected from the 1970s. There are two reasons

for this. First, I was able to collect a richer and nationally more representative data file than was

available to Lave and Seskin. Second, one of the themes of this talk is that quasi-experimental

techniques may provide a solution to many of the specification problems that plague the

traditional approach and I will later present some results from a quasi-experiment in the early

1970s. Thus, by focusing on this period I can hold the sample fixed across the different

statistical approaches.

A few other points about the subsequent results bear noting. In particular, this subsection

focuses on the effect of total suspended particulates (TSPs) on infant mortality. The focus on

infant mortality has a few benefits. For starters, the problem of unknown lifetime exposure to

pollution is significantly mitigated, if not solved, by the low migration rates of pregnant women

and infants.6 Here, pollution levels are assigned to infants based on the level of pollution in the

year of birth so this approach measures the exposure of the mother during the gestational period

6 It is possible that a mother’s lifetime exposure to air pollution, and not just exposure while pregnant, may also impact infant health. In this case, we have mitigated the lifetime exposure problem but not solved it.

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and the exposure of the newborn during the first few months after birth.7 In addition, given that

the mortality rate is higher in the first year of life than in the next 20 years combined (NCHS

1999), it seems reasonable to presume that infant deaths represent a large loss in life

expectancy.8 It is noteworthy that Lave and Seskin also analyzed the effect of air pollution on

infant mortality but did not motivate the analysis as a potential solution to the lifetime exposure

problem.

An additional issue is that the only measures of air pollution are the annual averages of

TSPs across counties. This is because the EPA’s monitoring program for TSPs was much more

pervasive than for any other air pollutant. In fact, only 10 out of the 501 observations in the

subsequent sample were monitored for all of the primary pollutants regulated by the Clean Air

Act in the early 1970s. It is notable though that TSPs is widely believed to be the most

dangerous form of air pollution.

This section also reviews Lave and Seskin’s results. This review demonstrates their

extensive and laudable efforts to test for a relationship between air pollution and human health

with the traditional epidemiological approach. It also highlights that mine and Lave and Seskin’s

results are similar in finding a fragile relationship between air pollution and human health.

A. Estimates of the Infant Mortality/TSPs Relationship from Cross-Sectional and Fixed Effects

Regressions Based on 1971 and 1972 Data

7 Data limitations from this period precluded using higher frequency (e.g., daily) TSPs and infant mortality data. 8 Relative to the adult mortality studies, another advantage of an analysis which focuses on infant deaths within 1-day, 1-month, and 1-year of birth is that it circumvents the measurement problem of unpredictable time delays (“delayed causation”) in the impact of pollution exposure on eventual death.

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This subsection presents some estimates of the association between infant mortality and

TSPs based on cross-sectional and fixed effects regressions that are similar to those estimated by

Lave and Seskin.9 For the 1971 and 1972 cross-sections, Table 2 presents the regression

estimates of the effect of TSPs on the number of internal infant deaths within a year of birth per

100,000 live births.10 Column 1 presents the unadjusted TSPs coefficient, while the remaining

columns correspond to specifications that include additional sets of controls. The sample sizes

and R2’s of the regressions are shown in brackets.

There is wide variability in the estimated effects of TSPs, both across specifications for a

given cross-section and across the cross-sections for a given specification. Both of the Column 1

estimates are positive, although neither would be judged statistically significant at conventional

levels. Taken literally, they imply that a 1 µg/m3 reduction in TSPs would reduce the infant

mortality rate by 1.6 and 0.9 per 100,000 live births. The associated elasticities are

approximately .089 and .045, respectively. Including the basic control variables available in the

Natality data in Column 2 has a noticeable effect on the point estimates in most years, even as

the precision of the estimates increases due to the greatly improved fit of the regressions.11

Columns 3-5 present the results from specifications that include additional Natality

variables and controls for per-capita income and earnings, employment, transfer payments,

Medicaid receipt, and state fixed effects. In Column 5, which includes state fixed effects, the

estimated effect of TSPs is positive and statistically significant in the 1971 cross-section but is

negative and statistically significant in 1972. The latter estimate is perversely signed and implies

9 These results are taken from Chay and Greenstone (2002). 10 The internal infant mortality rate is the mortality rate due to health-related causes of death (i.e., 8th International Classification of Diseases codes (ICD) 001 through 799) and excludes non-health related “external” causes (i.e., 8th ICD codes from 800 through 999). 11 The control variables included in the “Basic Natality” and “Unrestricted Natality” sets of variables are listed in the Data Appendix.

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that 1 µg/m3 reduction in TSPs would increase the infant mortality rate by 1.7 per 100,000 live

births. Notably, it is possible to get negative and positive point estimates in each cross-section.

Overall, there is little evidence of a systematic association between particulates pollution

and infant survival rates in these cross-sectional regressions. Further, the results are very

sensitive to the year analyzed and the set of variables used as controls. The sensitivity of the

results is disturbing and undermines confidence in this approach. A reasonable conclusion is that

the cross-sectional equations are subject to severe misspecification

The third panel of Table 2 presents the fixed effects estimates of the association between

mean TSPs and internal infant mortality rates based on first-differenced data from 1971-72. The

controls in each of the columns are exactly the same as in the first two panels except that they

too are first-differenced. The use of first-differenced data in the regressions eliminates the bias

in the cross-sectional estimates attributable to time-invariant omitted factors that vary across

counties.

The estimated TSPs coefficient in Column 1 is approximately the size of the 1972 cross-

sectional coefficient but is not statistically significant. Once the analysis regression adjusts, it is

evident that infant mortality rates and TSPs are essentially uncorrelated. The low R-squared

statistics reflect the difficulty in predicting changes in infant mortality.

Overall, it appears that the fixed effects association between TSPs and infant mortality is

small and sensitive to specification. These results are consistent with the possibility that the

fixed effects models are misspecified due to time-varying omitted variables and/or measurement

error. The results are also consistent with the possibility that there is not a causal relationship

between TSPs and infant mortality.

19

B. Lave and Seskin’s Estimates of the Health Effects of Air Pollution

It is informative to compare the previous results Lave and Seskin’s results. In their

book’s Table 4.1 (p. 54), they report the results of cross-sectional regressions from 1960 and

1961. In these regressions, the SMSA-level infant mortality rate is the dependent variable and

the explanatory variables are SMSA-level measures of total suspended particulates, sulfates, the

population density, the fraction of the population that is over 65, the fraction of the population

that is nonwhite, the poverty rate, and the population. This specification is relatively

parsimonious and is not directly comparable to any of the ones in Table 2 due to differences in

data availability.

Nevertheless, their estimates suggest that a 1 µg/m3 reduction in TSPs is associated with

a 1.3 – 2.1 fewer infant deaths per 100,000 live births. The associated elasticities range between

.061 and .097. These are similar to the unadjusted cross-sectional estimates in Table 2 of this

paper but generally differ from the adjusted estimates. The elasticity for their preferred measure

of airborne sulfates ranges between -.002 and .033.

Notably, Lave and Seskin’s particulates estimates all border on statistical significance at

conventional levels when the OLS formula for the standard errors is used. However, this

formula does not account for the possibility of heteroskedasticity. As a point of comparison,

both the Column 1 and 2 estimates in Table 2 for the 1971 cross-section would be judged

statistically significant by conventional criteria with the OLS formula but not with Eicker-White

formula that accounts for unspecified heteroskedasticity and is used in Table 2.

In their Table 8.3 (p. 171), Lave and Seskin report the results from pooled OLS

estimation on 26 SMSAs from the 1960-69 period. These estimates rely on both permanent

20

variation across SMSAs and time-series variation within SMSAs. They report the results from 3

separate specifications that control for the overall U.S. infant mortality rate, a linear time trend,

and time dummies, respectively, in order to account for secular changes in infant mortality. The

elasticity for their preferred measure of sulfates ranges from -.006 to -.004, implying a

“perverse” relationship. And, the elasticity for the preferred measure of TSPs ranges from .048

to .057.

Interestingly, Table 8.3 does not report the results from regressions that include SMSA

fixed effects that would control for all permanent SMSA-level determinants of infant mortality.

They text contains the following passage explaining this choice

Indeed, when the SMSA and time dummy variables were included, the estimated

coefficients of the air pollution variables were statistically nonsignificant in

explaining the…mortality rates (the coefficients were generally negative as well).

As a consequence of these preliminary findings, we chose to exclude the SMSA

dummy variables in the subsequent investigation (p. 166).

Thus, these results may be biased due to permanent unobserved factors and are not comparable

to the first-differenced results reported above.

Another feature of Lave and Seskin’s analysis is their extensive efforts to test their

hypothesis in a variety of settings. In addition to the analysis of infant mortality, they separately

examine the effects of air pollution on: age-sex-race specific mortality rates of adults; disease

specific mortality rates that air pollution might plausibly affect (e.g., respiratory cancers and

cardiovascular disease); and as a falsification exercise disease-specific mortality rates for

diseases for which there is not a plausible relationship (e.g., suicides and venereal diseases).

They also test the effects of daily air pollution on daily mortality rates. As they note, this

21

approach solves many omitted variables problems but introduces a new set of confounders (e.g.,

climate) and the “harvesting” problem discussed above.

The evidence from all of these other approaches is broadly similar to the infant mortality

results. That is, Lave and Seskin find modest associations between air pollution and the causes

of mortality that are plausibly related to air pollution. They summarize their results by writing,

“Not all the factors hypothesized to affect mortality were controlled in the analysis, but

considerable evidence supports the hypothesis that the relationship between the mortality rates

and our air pollution measures is causal” (p.241).

With the benefit of 25 years, my read of their tables is much less favorable regarding a

causal interpretation. I am disturbed by the sensitivity of their point estimates to the chosen

specification and think the estimates are likely plagued by omitted variables bias due to the

parsimonious specifications. Moreover, I suspect that that the standard errors of their regression

parameters are understated and that if calculated correctly there would be few significant

associations.

C. Summarizing the Results of the Traditional Epidemiological Approach

This section has presented evidence on the cross-sectional and fixed effects relationships

between infant mortality from my research with Kenneth Chay (Chay and Greenstone 2002) and

reviewed Lave and Seskin’s results. Together these results fail to provide compelling evidence

of a strong association between TSPs and human health. In general, the results are highly

sensitive to the year of the sample and to the exact specification that is estimated. This is best

summarized in Column 5 of Table 2 where the most robust specification produces a statistically

22

significant positive association between infant mortality and TSPs in 1971 and a statistically

significant negative association in 1972.

The point is that no matter how extensive the data collection, the estimated parameters

are only as reliable as the econometric assumptions that underlie them. These assumptions are

not testable and may be unlikely to hold. Overall, I conclude that traditional epidemiological

estimates of the relationship between TSPs and infant mortality are contradictory and do not

provide and fail to answer whether this relationship is causal.

IV. The Quasi-Experimental Approach

If traditional epidemiological/regression estimates are unlikely to allow for the

identification of a causal relationship between human health and air pollution, what alternatives

are available? The ideal solution to this problem of inference is to run a classical experiment

where individuals are randomly assigned to a group that is exposed to a specified concentration

of air pollution or to a group that is exposed to “clean” air. Due to the random assignment the

groups should be identical on all dimensions except exposure to air pollution. Thus, the “clean”

group can serve as a counterfactual for what would have happened to the group exposed to the

air pollution in the absence of this exposure. Consequently any differences in health outcomes

can be attributed to the differences in air pollution.

A. What is a Quasi-Experiment?

23

Of course, such experiments are not ethical in the case of air pollution and this paper’s

primary argument is that the quasi-experimental approach is a valuable means to obtain reliable

estimates of the effect of air pollution on human health. In a quasi-experimental evaluation, the

researcher exploits differences in outcomes between a treatment group and a control group, just

as in a classical experiment. In the case of a quasi-experiment, however, treatment status is

determined by nature, politics, an accident, or some other action beyond the researcher’s control.

Despite the “nonrandom” nature of the treatment status, it may still be possible to draw valid

inferences from the differences in outcomes between the treatment and control groups. The

validity of the inference rests on the assumption that the assignment to the treatment and control

groups is not related to other determinants of human health. In this case, it is not necessary to

specify and correctly control for all the confounding variables, as is the case with the more

traditional epidemiological/regression approach.

In the case of air pollution, an ideal quasi-experiment is an event that alters one group’s

exposure to air pollution but leave the concentration of air pollution faced by another group(s)

unaltered. Moreover, this event cannot affect other determinants of human health. As an

example of a valid quasi-experiment, consider a government mandated adoption of a new TSPs

abatement technology by all TSPs emitters that reduces their emissions to zero but does not

affect their production costs. Moreover, assume that this forced adoption occurred in one area

but not another and that the two areas and their populations were identical in advance of the

adoption. A simple post-adoption comparison of the health outcomes in the two areas would

provide a causal estimate of the effect of TSPs.

B. Threats to the Validity of Quasi-Experiments

24

In conducting a quasi-experiment, it is important to be aware of the potential pitfalls

associated with this approach that may undermine a causal interpretation of the results. In their

classic work, Cook and Campbell (1979) call these pitfalls “threats to validity,” where validity is

the truth of a proposition or conclusion.12 They divide these into threats to internal, external, and

construct validity.13

Internal validity refers to whether it is possible to validly draw the inference that the

difference in the dependent variables is due to the explanatory variable of interest. Cook and

Campbell (1979) and Meyer (1994) provide exhaustive lists of these threats, but I think they can

largely be summarized as instances when treatment status may be related to the post-treatment

outcome for reasons other than the treatment. This could be due to omitted variables, inadequate

controls for pre-period trends, and/or the determination of the selection rule. As an example,

suppose that the new abatement technology was introduced in a particular area because it was

known that this area was going to have deterioration in human health outcomes and the reduction

in TSPs was intended to counterbalance this deterioration. In this case, the estimated treatment

effect will measure the effect of TSPs plus the deterioration in health that would have occurred in

the absence of the treatment.14

External validity refers to whether a quasi-experiment’s results can be generalized to

another context. People, places, or time are the three major threats to external validity. As an

example, the individuals in the treatment group may differ from the overall population (perhaps

12 These “threats to validity” apply to all empirical studies, but this subsection discusses them in the context of quasi-experiments. 13 This subsection draws on Cook and Campbell (1979) and Meyer (1994). 14 Other threats to internal validity include misspecified variances that lead to a biased standard errors, sample attrition, and changes in data collection that cause changes in the measured variables.

25

they are more sensitive to air pollution) so that the estimated treatment effects are not

informative about the effect of the treatment in the overall population. Or, the estimated

treatment effect may differ across geographic or institutional settings. Or, the treatment effect

might not be the same in a different year (e.g., if in the future a pill is invented that protects

individuals from air pollution, then the abatement technology would have a different effect).15

An issue that is closely related to external validity is that a treatment’s effect may depend

on whether it is implemented on a small or large scale. This could be relevant in the case of air

pollution and human health if people have sorted themselves into locations of the country based

on the sensitivity of their health to air pollution. The point is that if the estimated treatment is

derived from a subset of the population whose sensitivity differs from the average person’s, then

a national policy would have different effects. See Heckman (??) on the estimation of treatment

effects in the presence of heterogeneity and compensatory behavior.

Finally, construct validity refers to whether the researcher correctly understands the

nature of the treatment. Returning to the example of the new abatement technology, suppose

that, in addition to removing all TSPs emissions, it also reduces emissions of all other air

pollutants to zero. If these other pollutants are important predictors of human health, then a post-

adoption comparison of human health in the two areas would be unable to separate the effect of

TSPs from the other air pollutants. In this case, the researcher’s inadequate understanding of the

treatment would cause her to conclude that TSPs affect human health when in fact the effect on

human health is due to reduction of all air pollution. Notably, it is still possible to obtain

unbiased estimates of the overall effect of the new abatement technology—that is, the properly

understood treatment.

15 See Imbens and Angrist (1994) and Heckman and Vytlacil (1999) on the interpretation of instrumental variables estimates in the presence of heterogeneous responses.

26

C. Can these Pitfalls be Avoided?

The prior discussion naturally raises the question of how to find a valid quasi-experiment.

Unfortunately, there is not a handy recipe or statistical formula that can be taken off the shelf.

Since the treatment in a quasi-experiment is never assigned randomly, they are by their very

nature messy and lack the sharpness and reliability of a classical experiment. Consequently, the

keys to a good quasi-experimental design are to be paranoid about the threats to its validity and

to leave no stone unturned in an effort to test whether its assumptions are valid. Although these

assumptions can never be proven, hard work or, as the statistician David Freedman calls it,

“Shoe Leather” can help to understand the source of the variation that determines the explanatory

variable of interest and, in turn, a quasi-experiment’s validity (Freedman 1991).

An potentially convincing feature of a quasi-experiment is if the observable covariates

are balanced across the treatment and control groups. If this is the case, then it is unnecessary to

adjust the treatment effect for observables and functional form concerns are no longer relevant.

Even if this is not the case, an examination of the distribution of the observables across the

treatment and control groups can identify the likely sources of confounding that might inform the

choice of a statistical model. In assessing the balance, it is frequently important to collect new

data sets or use less well known ones.

The balancing of the observables does not guarantee the internal validity of a quasi-

experiment, because the unobservables may differ across the treatments and controls. Economic

reasoning or models can often help to identify cases where this is especially likely to be the case.

For example, a thorough understanding of how the treatment was assigned might identify that

27

individuals with a particular characteristic (e.g., susceptibility to air pollution-related health

problems) are more likely to receive the treatment and this could threaten the internal validity.

A thorough understanding of the assignment rule and the treatment can also help to assess

the external and construct validity. For example, we might be interested in determining the

effect of a nationwide 10% reduction in TSPs. But the available quasi-experiments might be

based on areas of the country with high concentrations of TSPs. If individuals sort themselves

across the country based on their susceptibility to TSPs, then the results of such a quasi-

experiment would not be informative about the health effects in relatively clean areas.

Alternatively if TSPs does not affect human health below some concentration, then estimates of

the gradient at high concentrations will not answer the broader question. Regarding construct

validity, if the treatment (e.g., an abatement technology) affects multiple pollutants then the

available quasi-experiment is unable to provide an estimate of the effect of the reduction in

TSPs.

In summary, the appeal of the quasi-experimental approach is that it relies on transparent

variation in the explanatory variable of interest. Of course, the transparency of the variation (or

the mere labeling of the variation as a quasi-experiment) does not guarantee that the threats to its

validity are satisfied. Through expenditures of “Shoe Leather”, it may be possible to determine

whether the variation is exogenous or at least to narrow the range of plausible explanations. As

Meyer (1994) wrote, “If one cannot experimentally control the variation one is using, one should

understand its source.”

D. Can the Quasi-Experimental Approach Answer Important Questions?

28

As I have discussed above, quasi-experiments are determined by nature, politics, an

accident, or some other action beyond the researcher’s control. A key limitation of this approach

to research is that there is no guarantee that these actions will help to inform the questions that

we find most interesting. This can place researchers in the uncomfortable position of letting

nature set their research agendas. This is frustrating because it raises the possibility that the most

important causal questions remain unanswerable and has led some to question the value of the

quasi-experimental approach.16 I find this criticism unconvincing for at least two reasons.

The first reason is that the quasi-experimental approach has proven to be very successful

in deepening the understanding of causal relationships in a variety of settings. An exhaustive

listing is beyond the scope of this paper, but one would include quasi-experiments that estimate:

how cholera is transmitted (Snow 1855); the effects of anti-discrimination laws on African-

American’s earnings (Heckman and Payner 1989 and Chay 1998); the labor supply

consequences of unemployment insurance benefits (Meyer 1990); the effect of minimum wage

laws (Card and Krueger); the returns to an additional year of schooling (Angrist and Krueger

1991; Ashenfelter and Krueger 199?; Card miles 199?); the effect of military service on earnings

(Angrist 1990); individuals’ willingness to pay for school quality (Black 199?); individuals’

willingness to pay for clean air (Chay and Greenstone 2000); as well as the effects of air

pollution on human health (Ransom and Pope 1995 and Chay and Greenstone 2002a and 2002b).

The point is that carefully chosen quasi-experiments can yield insights on important questions.

My second disagreement with this criticism of the quasi-experimental approach is that it

is unfair to consider the absence of the ideal quasi-experiment as a shortcoming of this approach.

Rather, I think this is a statement that for many of the most interesting questions, it is not

16 See Freedman (1991a and 1991b) for a criticism of the regression approach to testing causal propositions.

29

possible to produce empirical evidence of a causal relationship. The absence of a quasi-

experiment does not make it any more likely that an alternative research strategy is likely to

produce convincing evidence of a causal relationship. Knowing the difference between

questions that can be empirically tested and those that cannot is a crucial element in scientific

advancement.

Of course, this does not mean that questions for which valid quasi-experiments are

unavailable should not be researched. Society frequently has to make decisions (e.g., should we

regulate emissions of mercury into the air?) in the absence of causal evidence. The point is that

when we research these questions it is important to be clear that the resulting evidence is not a

meaningful test of the causal proposition that underlies the question. This idea was captured by

Trygve Haavelmo almost 60 years ago when he wrote that when we test theories for which an

experiment is unavailable, “we can make the agreement or disagreement between theory and the

facts depend upon two things: the facts we choose to consider, as well our theory about them” (p.

14, Haavelmo 1944).

V. Two Applications of Quasi-Experiments to Human Health and Air Pollution

This section reviews two quasi-experiments that have provided the relationship between

air pollution and human health. I describe each paper’s approach and results. I also provide an

interpretation section that discusses each quasi-experiment in the context of Cook and

Campbell’s threats to validity.

A. Chay and Greenstone’s “Air Quality, Infant Mortality, and the Clean Air Act of 1970”

30

This paper uses differential air quality changes induced by federal air pollution

regulations as the basis for a quasi-experiment that examines the effect of total suspended

particulates (TSPs) on infant mortality. The 1970 Clean Air Act Amendment (CAAA) marked

an unprecedented attempt by the federal government to mandate lower levels of pollution. The

centerpiece of the 1970 CAAA was the establishment of National Ambient Air Quality

Standards that were applied at the county level. If pollution concentrations in a county exceed

the federal ceiling, then the EPA designates the county as nonattainment for that pollutant.

Polluters in nonattainment counties face much stricter regulatory oversight than their

counterparts in attainment counties. For TSPs pollution a county is nonattainment if either of

two thresholds is exceeded in the previous year: 1) the annual geometric mean concentration

exceeds 75 µg/m3, or 2) the second highest daily concentration exceeds 260 µg/m3.

In an earlier paper, Chay and Greenstone (2000) established that nonattainment status is

associated with sharp, large reductions in TSPs during the 1970s. Their idea in the current paper

is to test whether these regulation-induced improvements in air quality are associated with

changes in infant mortality. This is done by using nonattainment status as an instrument for

1971-2 changes in TSPs in equations for changes in infant mortality rates. Thus, this quasi-

experiment is based on the first year (1972) that this legislation was in force.

There are several reasons that the air pollution reductions induced by the 1970 Clean Air

Act may be a valid quasi-experiment with which to estimate the TSPs-infant health relation.

First, it is plausible that federally mandated regulatory pressure is orthogonal to county-level

changes in infant mortality rates, except through its impact on air pollution, so nonattainment

status may be a valid instrument.

31

Second, nonattainment status is a discrete function of the previous year’s TSPs levels.

This discontinuity in the assignment of regulations can be used to gauge the credibility of the

research design. Thus, the assignment of the regulations has the feature of a quasi-experimental

regression-discontinuity design (Cook and Campbell 1979). If the unobservables are ‘smooth’ at

the regulatory thresholds, then comparing outcome changes in nonattainment and attainment

counties with similar pre-regulation TSPs levels will control for all omitted factors correlated

with TSPs. Under this assumption discrete differences in mean outcome changes between

nonattainment and attainment counties near the federal ceilings are attributable to the

regulations. The discontinuity in the assignment of regulations provides a unique opportunity to

gauge the credibility of the quasi-experiment and develop convincing tests of causality.

Data Sources

The paper brings together an unprecedented amount of unique and comprehensive data

on county-level air pollution, pollution regulations, infant births and deaths, and other potential

determinants of infant health. This database allows for a much broader examination, both across

sites and over time, than has previously been conducted. Further, the comprehensive set of

control variables allows the authors to adjust the estimates for many of the likely omitted

variables bias

The health outcome variables and a number of the control variables come from the

National Mortality Detail Files and National Natality Detail Files, which are derived from

censuses of death and birth certificates. The individual birth and infant death records are merged

at the county level for each year to create county by year cells. For each cell, the infant mortality

rate is calculated as the ratio of the total number of infant deaths of a certain type (age and cause

32

of death) to the total number of births. Mortality rates within 24 hours, 28 days, and 1 year of

birth are computed separately for each year. The authors also calculate separate mortality rates

for deaths due to internal health reasons and deaths due to external “non-health” related causes

such as accidents and homicides.17 The authors assume that there is no causal pathway linking

air pollution to external causes of death, so the estimated association between external mortality

rates and TSPs pollution is used as a check on the internal consistency of the findings.18 19 This

is similar in spirit to Lave and Seskin’s testing for an association between air pollution and

venereal diseases and suicides.

The microdata on the control variables available in the Natality Files are also aggregated

into annual county cells. The detailed Natality variables fall into four categories: socioeconomic

and demographic characteristics of the parents; medical system utilization, including prenatal

care usage (Rosenzweig and Schultz 1983; Institute of Medicine 1985); maternal health

endowment, such as mother’s age and pregnancy history (Rosenzweig and Schultz 1983;

Rosenzweig and Wolpin 1991); and infant health endowment. The annual, monitor-level data on

TSPs concentrations were obtained by filing a Freedom of Information Act request with the

EPA. These data are used for measures of ambient concentrations and to determine

nonattainment status.

The authors also collected a variety of county-level economic variables data as controls.

They include annual measures of: per-capita income, per-capita net earnings, the employment to

17 “Internal” and “external” deaths span all possible causes of death. Deaths with 8th International Classification of Diseases (ICD) codes from 001 to 799 are classified as internal, while those with ICD codes from 800 to 999 are in the external category. 18. That is, the association between TSPs and external infant deaths may result from unobserved secular factors that affect all types of infant death. 19 See Utell and Samet (1996) for a summary of the evidence on the pathophysiological relationship between TSPs and human health.

33

population ratio, the manufacturing employment to population ratio, total transfer payments;

total medical care payments; public expenditures on medical care for low-income individuals

(primarily Medicaid and local assistance programs); income maintenance benefits; family

assistance payments, including AFDC; Food Stamps payments; and Unemployment Insurance

benefits.

Econometric Model

Consider, the first-differenced versions of the cross-sectional equations from (1) and (2)

for the years 1971and 1972:

(4) yc72 - yc71 = (Xc72 - Xc71)′β + θ(Tc72 - Tc71) + (uc72 - uc71)

(5) Tc72 - Tc71 = (Xc72 - Xc71)′Π + (vc72 - vc71).

Consistent estimation of θ, the parameter on the TSPs variable, requires E[(uc72 - uc71)(vc72 –

vc71)]=0. This assumption may not hold due to changes in omitted variables or mismeasurement

of the TSPs variables.

Now, suppose there exists an instrumental variable, Zc, which causes changes in TSPs

without having a direct effect on infant mortality rate changes. Such a variable would purge the

estimates of the bias associated with the covariance between unobserved shocks to TSPs levels

and unobserved shocks to infant mortality rates and the measurement error. One plausible

instrument is the 1970 CAAA regulatory intervention for TSPs, measured by the attainment-

nonattainment status of a county. Equations (6) and (7) describe this relationship formally:

(6) Tc72 - Tc71 = (Xc72 - Xc71)′ΠTX + Zc71ΠTZ + (vc72 - vc71)°, and

(7) Zc72 = 1(Tc70 > T ) = 1(vc70 > T - Xc70′Π - λc),

34

where Zc72 is the regulatory status of county c in 1972, 1(•) is an indicator function equal to one

if the enclosed statement is true, and T is the maximum concentration of TSPs allowed by the

federal regulations. Regulatory status in 1972 is a discrete function of 1970 pollution levels.

Further, if T and are the annual geometric mean and 2nd highest daily TSPs

concentrations, respectively, then the actual regulatory instrument used is 1( > 75 µg/m3 or

avg70c

max70cT

avg70cT

> 260 µg/m3). max70cT

Two sufficient conditions for the instrumental variables (IV) estimator (θIV) to provide a

consistent estimate of the effects of TSPs are ΠTZ ≠ 0 and E[vc70(uc72 - uc71)] = 0. The first

condition holds if the regulations induced air quality improvements. The second condition

requires that unobserved mortality rate shocks from 1971-72 are orthogonal to transitory shocks

to 1970 TSPs levels.

Even if E[vc70(uc72 - uc71)] ≠ 0, causal inferences on θ may be possible by leveraging the

regression discontinuity (RD) design implicit in the 1(•) function that determines nonattainment

status. For example if [vc70(uc72 - uc71)]=0 in the neighborhood of the regulatory ceiling (i.e., 75

µg/m3), then comparison of changes in nonattainment and attainment counties in this

neighborhood will control for any omitted variables. In the case where this assumption is invalid

but the relationship between vc70 and (uc72 - uc71) is sufficiently smooth, then causal inference is

possible by including smooth functions of Tc70 in the vector of covariates.

Graphical Results

The analysis begins with a graphical examination of the effect of TSPs nonattainment

status on the 1971-2 change in TSPs and internal infant mortality rates. Figure 1 graphs the

bivariate relation between either the change in TSPs or the change in infant mortality with the

35

geometric mean of TSPs levels in 1970 (the regulation selection year). The plots result from the

estimation of nonparametric regressions for the 1971-72 changes in TSPs and infant mortality

rates as a function of the 1970 geometric mean TSPs using a uniform kernel density regression

smoother.20 The intention is to examine whether there are sharp differences in the dependent

variables that correspond to the sharp change in the probability that a county was designated

nonattainment. Recall, counties with 1970 geometric mean TSPs levels below (above) 75 µg/m3

are attainment (nonattainment) in 1972

The figure presents these conditional mean changes for the universe of counties in our

primary sample.21 It documents that nonattainment counties experienced much larger reductions

in mean TSPs and infant mortality rates from 1971-72 than their attainment counterparts that had

1970 mean TSPs less than 75 µg/m3. It is also evident that the TSPs reductions were greater in

counties with higher levels of TSPs in the regulation selection year.

The most striking features of the graph are the clear “trend breaks” in TSPs and infant

mortality rate changes at the regulatory threshold. While it is possible that these trend breaks are

due to an unobserved factor, such a factor must change as discretely as the function that

determines nonattainment status. In the absence of such an explanation, the trend breaks suggest

that regulation is a causal factor. On the other hand, there appear to be secular decreases in

infant mortality rate reductions at 1970 TSPs levels well below (30-50 µg/m3) and well above

(100-150 µg/m3) the 75 µg/m3 threshold.

20 Counties that were nonattainment in 1972 for exceeding the daily concentration standard but not the annual geometric mean standard in 1970 are dropped from the analysis. Thus, the sample contains 264 nonattainment counties and 230 attainment ones. Also, note that the regressions do not adjust for other covariates. 21 The smoothed scatterplots are not very sensitive to the bandwidth choice.

36

This figure is also valuable because it nonparametrically displays the data, making it

possible to obtain local “eyeball” instrumental variables estimates of the effect of TSPs on infant

mortality. Consequently, it previews the instrumental variables estimates that are presented in

the next section. The set of counties in the neighborhood of the regulation threshold (e.g.,

counties with 1970 geometric mean TSPs between 50 and 100 µg/m3) may be of especial

interest. In these counties, there is a clear association between larger reductions in mean TSPs

and greater decreases in infant mortality. Further, the correspondence of the trend breaks

suggests that near the regulatory ceiling, the research design may identify the casual relationship

between air pollution and infant mortality through the mechanism of regulation. The relatively

smaller declines in infant mortality in counties with 1970 TSPs greater than 100 µg/m3 indicate

that θIV will be of a smaller magnitude when it is estimated from the entire sample. This may be

due to either omitted variables or a nonconstant gradient.

Statistical Results

Table 3 presents the instrumental variables estimates of the effect of TSPs pollution on

internal infant mortality rates within one year of birth. Here, the indicator for 1972

nonattainment status is used as an instrument for 1971-72 changes in TSPs. The first column

presents the unadjusted estimate (i.e., the Wald estimate), while the remaining columns

correspond to specifications that include additional sets of controls, as in Table 2.

In Column 1, the estimated TSPs effect is highly significant and implies that a 1-µg/m3

decline in TSPs results in 4.8 fewer infant deaths per 100,000 live births. When a limited set of

controls from the Natality files are added in Column 2, the estimated TSPs coefficient rises to 6.1

and remains significant at well below the 1-percent level. The specifications in Columns 3 and 4

37

add a fuller set of controls from the Natality files, an unrestricted year effect, and the per-capita

income, earnings, and transfer payments variables. The point estimate rises to 7.8-8.5. Since the

sampling errors are much larger, these estimates are significant at the 5-percent and 10-percent

levels.

Finally, the specification in Column 5 includes unrestricted state-year effects, which

absorb all unobservables that vary across states from 1971-72. In this saturated model, the

treatment effect is identified using only comparisons of changes between attainment and

nonattainment counties within the same state. The TSPs estimate rises to 16.8 and is significant

at conventional levels, although it is much less precise.

The results in Table 4 are based on the implementation of the regression discontinuity

approach. This is done by presenting the instrumental variables estimates of the TSPs effects for

various subsamples of counties with 1970 geometric mean TSPs near the nonattainment

threshold. The first two columns show the estimates for the entire sample of counties,

unadjusted and adjusted for the basic Natality controls, respectively. The remaining columns

present unadjusted and adjusted estimates for subsamples of counties with 1970 mean TSPs

ranging from 30-150, 50-100, 60-90, and 65-85 µg/m3, respectively. The idea is to progressively

cut the sample so that it is more and more focused on the counties in the neighborhood of the

regulatory threshold, where all else may be held equal.

These results are striking. As the sample is limited to counties with 1970 pollution levels

closer to the regulatory threshold, the estimated effect of 1971-72 mean TSPs changes increases

monotonically. This is consistent with the patterns depicted in Figure 1. The adjusted estimates

for counties with 1970 TSPs levels between 30-150, 50-100, and 60-90 µg/m3 are all significant

at conventional levels, even as the sample sizes fall to 428, 276, and 173, respectively. They

38

imply that a 1-µg/m3 TSPs reduction results in 7.2-11.6 fewer infant deaths per 100,000 live

births. The estimates do not change when the sample is limited to the 120 counties with 1970

TSPs levels between 65-85 µg/m3, although the sampling errors double.22

It is instructive to compare these results to the cross-sectional and fixed effects estimates

shown in Table 2. They are based on identical samples and specifications. The instrumental

variables estimates of the TSPs effect are much larger in magnitude, significant, and fairly stable

across specifications. The weighted average of these estimates is approximately 7, when the

weight is the inverse of the standard error. This suggests that a 1-µg/m3 decline in TSPs is

associated with 7 fewer infant deaths per 100,000 live births, which is an elasticity of 0.4. This

is about 3.5 times greater than the largest cross-sectional estimate in Table 2 and is similar to the

estimated effect that Chay and Greenstone found in an earlier paper (1999). Overall, the relative

stability of the estimates across specifications and the trend breaks in Figure 1 suggest that the

design may be revealing a causal effect of particulates pollution.

Estimates of the Benefits of TSPs Reductions

Overall, it appears that the 1970 Clean Air Act Amendments resulted in substantial health

benefits for infants during the first year that it was in force. This subsection monetizes these

health improvements and discusses their implications for the optimal design of particulates

regulations.

In 1972 there were over 1.5 million births in the nonattainment counties in our sample.

These counties experienced a relative reduction in TSPs of 11 µg/m3. With an estimated

22 In each case, nonattainment counties account for about half of the sample. For example, there are 58 attainment and 62 nonattainment counties with 1970 geometric mean TSPs between 65-85 µg/m3.

39

reduction in infant mortality of 7 per 100,000 live births for a 1 µg/m3 reduction in TSPs, our

estimates imply that roughly 1,200 fewer infants died in 1972 than would have in the absence of

the CAAAs. When a statistical life is valued at $1.6 million to $8.5 million ($1997), this

reduction in infant mortality is worth approximately $1.9-10.2 billion ($1997).23 To the extent

that this reduction in TSPs was permanent, these benefits would have accrued in each of the 30

years since then. In this case assuming a 5% discount rate, the present discounted value of these

health improvements in 1971 ranged between $31-165 billion ($1997). This calculation ignores

the other health and aesthetic benefits associated with lower pollution levels, so it likely to

understate the total economic value of the regulation-induced TSPs reductions.24

These results may also be informative about the form of the optimal particulates standard.

The EPA’s standard of 75 µg/m3 for annual geometric mean TSPs concentrations was chosen to

“protect the public health”. The optimality of this standard depends on the form of the infant

mortality-TSPs gradient and whether the marginal cost of abating TSPs varies with the ambient

concentration of TSPs.25

Taken literally, Figure 1 implies that although there are significant health benefits to a

reduction in TSPs at very high concentrations, the marginal benefit of a unit change is greater at

TSPs levels below 100 µg/m3. Specifically, Table 4 shows that a unit reduction in TSPs results

in about 12 fewer infant deaths per 100,000 live births at TSPs concentrations slightly above 75

23 Viscusi’s (1993) review of the literature suggests that the value of a statistical life ranges from $3.5 - $8.5 million ($1997), but recent research by Ashenfelter and Greenstone (2002) indicates that it may be less than $1.6 million ($1997). Also see Johansson (2001) on the value of a statistical life. 24 Chay and Greenstone (2000) use a hedonic analysis to value a similar reduction in mean TSPs associated with nonattainment status in the mid-1970s. They calculated a $65 billion ($1997) willingness-to-pay for this change. 25 See Henderson (1996), Becker and Henderson (2000), and Greenstone (2002) on the costs of the Clean Air Act Amendments in the manufacturing sector.

40

µg/m3. Although the Clean Air Act quasi-experiment does not allow for identification below the

threshold, Chay and Greenstone (1999) document that TSPs have substantial effects on infant

health at concentrations below 75 µg/m3. This suggests that a federal air quality standard below

75 µg/m3 could provide greater health benefits to the public.

B. Ransom and Pope’s “External Health Costs of a Steel Mill”

This paper uses an improvement in air quality induced by the temporary closing of a steel

mill in Utah Valley, Utah as the basis for a quasi-experiment to examine the effect of the steel

mill’s operation on human health. The valley has a large, integrated steel mill near its center,

which is the valley’s principal source of particulate. The valley is prone to temperature inversion

during the winter, which cause the air to become stagnant, trapping pollutants near the valley

floor. During these inversions, the mill contributes 50-70 percent of total fine particulate (PM10)

pollution. On August 1, 1986, labor difficulties caused the mill to shut down and a new owner

reopened the mill 13 months later on September 1, 1987

During the winter months of this 13 month period, PM10 pollution was half its usual

level. Moreover, violations of the federal 24-hour PM10 standard occurred an average of 12.6

times per year in years that the mill operated and 0 times during the year of labor strife. The idea

of this paper is to compare health outcome (especially respiratory related ones) in the 13 months

that the steel mill was closed to the period before and after when the mill was operating in an

effort to measure its effect on health. Notably, PM10 concentrations are treated as “intermediate”

variable that are not of direct interest so the study does not provide evidence on the human

health-PM10 gradient.

41

There are several reasons that this may be a valid quasi-experiment to estimate the effect

of the steel mill’s operation on health. First, it is difficult to think of a reason that the timing of

the labor strike was related to patterns in health outcomes. Second, the authors use Cache

Valley, also in Utah, as a counterfactual to capture any time trends in health outcomes. Cache

Valley is similar to Utah Valley on a number of dimensions. Both areas are mountain valleys at

roughly the same elevation, have approximately similar climates, commonly experience severe

temperature inversions during the winter, have similar demographics, have low smoking rates,

and rely on natural gas as the primary source of residential heating.

There are some differences between the two valleys. Crucially, the Cache Valley is

unaffected by the steel plant’s emissions. Additionally, the Utah Valley, which contains the

cities of Provo and Orem, has a 1990 population of 223,800, while the Cache Valley’s

population is 70,200. The average pollution concentrations in the Cache Valley are roughly 1/3

to 1/2 the levels found in the Utah Valley.

One time-varying factor that may differ across the two valleys is the incidence of viral

bronchiolitis, a contagious disease, which is due to an infection in the lungs and increases

hospitalization rates for respiratory rates. Fumento (1997) claims that the closure of the steel

mill coincides with a year when the incidence of viral bronchiolitiis was especially low. If this

claim is correct, then the internal validity of the quasi-experiment is undermined.

Data Sources

In order to investigate the health consequences of the steel mill’s closure, the authors

collected data on morbidity and mortality. The measures of morbidity come from hospital

admissions records for respiratory and cardiovascular diseases from April 1, 1985 through April

42

30, 1991. These are based on the admissions records of 8 major acute care hospitals, including

all three acute care hospitals in Utah Valley, and the only hospital in Cache Valley. The records

contain the patients’ zip codes, which allow for the determination of whether they live in the

Utah Valley or Cache Valley. In order to obtain mortality information, the authors accessed the

Utah State Vital Statistics data from 1985 through 1989. These data are based on a census of

death certificates and importantly contain information on the deceased’s county of residence

Econometric Approach

The paper employs a difference in difference econometric approach. Equation (8)

captures the spirit of their approach:

(8) yct = Xvt′β + α 1 (Observation from Utah Valley)v

+ λ 1(Observation from Period when Steel Mill Closed)t

+ δ 1(Observation from Utah Valley when Steel Mill Closed)vt

+ εvt,

where yct is the number of hospital admissions or deaths in valley v (either Utah Valley or Cache

Valley) on day t, Xvt is a vector of observed determinants of y (population size, season of the

year, and a time trend), 1 (Observation from Utah Valley)v is an indicator variable that equals 1

for observations from the Utah Valley, 1(Observation from Period when Steel Mill Closed)t is an

indicator that equals 1 for observations from either valley when the mill is open, and

1(Observation from Utah Valley when Steel Mill Closed)vt is an indicator that equals 1 for

observations from the Utah Valley when the steel mill was closed, and εvt is the idiosyncratic

unobservable determinant of hospital admissions or deaths. Due to the count nature of the

dependent variable, equation (8) is estimated as a negative binomial regression.

43

δ is the parameter of interest. It captures the variation in the dependent variable that is

specific to the Utah Valley when the mill was closed after adjusting for the average incidence of

hospitalizations in the Utah Valley and any time component that is common to the Utah Valley

and the Cache Valley. The key identifying assumption is that unobserved, time-varying factors

(e.g., the incidence of viral bronchiolitiis) are not correlated with 1(Observation from Utah

Valley when Steel Mill Closed)vt.

Results

Table 5 presents daily averages of hospital admissions and mortality and the associated

standard errors for different categories of diseases. The data are reported separately for the Utah

and Cache valleys for periods with the steel plant open and closed. The intention is to compare

the period when the plant is closed to the period when it is open. The first row of the first

column shows that all age admissions for bronchitis and asthma were 0.188 higher in the Utah

Valley when the plant was open. Further, almost the entire increase was accounted for by higher

admissions rates for preschool aged children. This translates into about 60 additional admissions

per year. This is a dramatic increase. All age admission rates were actually higher in the Cache

Valley when the mill was closed and preschool admissions were modestly smaller. The closing

of the mill is also associated with lower rates of admissions for “Other Respiratory Diseases”.

However, the mill’s closure is not associated statistically meaningful changes in mortality rates

or admission rates for cardiovascular diseases and pneumonia.

Estimates of the External Costs of the Steel Mill

44

Table 6 provides some estimates of the annual excess hospitalization costs associated

with the operation of the steel mill in the Utah Valley by disease. Column 1 reports the

difference in differences estimator, δ, and its 95% confidence interval (in square brackets) from

the fitting of equation (8) with a negative binomial regression. Column 2 presents the average

hospitalization charge per admission in 1991$. Column 3 reports the results of multiplying the

Column 1 and 2 entries to derive an estimate of the total excess charges associated with the steel

mill’s operation. The final row contains the estimate of the total increase in hospital admissions,

which is obtained by summing across all four diseases categories.

The total row indicates that annual hospitalization costs are $2.07 million higher when

the steel plant is operating. This estimate has a 95% confidence interval of $90,000 to $4.05

million. Approximately 65% of the increase is due to cardiovascular diseases, while bronchitis

and asthma are also important contributors. It is not shown in Table 6, but the estimate that is

based on Utah Valley data only (this is a from an open versus closed comparison) is $1.966

million with a 95% confidence interval of $908,000 to $3.024 million. It is worth noting that

these figures exclude any additional costs associated with emergency room visits, out-of hospital

medication and health care, and restrictions on activities. Overall, the hospitalization estimates

suggest that residents of the Utah Valley bear external costs of over $1,000 per worker per year.

C. Discussion of the Threats to Validity in these Two Quasi-Experiments

[I still have to write this section, but what follows is a brief outline.]

Internal validity

45

C&G—specified a clear hypothesis (i.e., jump at regulatory threshold) and tested it. Better

balancing of observables, especially near the threshold. Lots of data collection

R&P—specified clear hypothesis (strike causes admissions to go down) and tested it. Would

like to see trends, in order to test for dynamics and other observable before the strike.

External validity

C&G—not identified at tsps levels below 75. two things undermine extrapolation: possible

sorting/compensatory behavior (although a sorting story would imply that people that are

especially sensitive are located in relatively clean area, so effects would be bigger there).and

nonlinear gradient.

R&P—very difficult to extrapolate, particularly w/o showing change in pm10’s.

Construct validity

C&G: Does tsps nonattainment status cause reduction in other air pollutants that affect infant

mortality?

R&P: is the treatment the strike or the reduction in air pollution

VI. Conclusions

46

A quarter century ago, Lester Lave and Eugene Seskin published their path breaking

book, Air Pollution and Human Health. This book was a conscious effort to try to produce

reliable estimates of the costs associated with air pollution in order to develop efficient

environmental policies. They wrote that society’s problem is to balance, “…the benefits that

polluters obtain from venting residuals against the damage that is incurred by society as a result

of the increased pollution. To find an optimum level, we must know the marginal benefits and

costs associated with abatement” (pp. 3-4). Their work and the work that it has inspired have

dramatically improved our knowledge of the health effects of air pollution.

This paper argues that the quality of the evidence on this important relationship can be

substantially improved through a greater reliance on quasi-experimental evaluation techniques.

This argument is motivated by the observed instability in the estimated health effects from

epidemiological/regression approaches and from the difficulty in proving or disproving the

assumptions that underlie them. In contrast, quasi-experiments generally rely on transparent

variation in the explanatory variable of interest. Of course, the transparency of the variation (or

the mere labeling of the variation as a quasi-experiment) does not guarantee that the threats to its

validity are satisfied. Through expenditures of “Shoe Leather”, it may be possible to determine

whether the variation is exogenous or at least to narrow the range of plausible explanations.

The air pollution/human health relationship is not the only area of environmental policy

where decisive evidence is missing. Consequently, the political debates on these issues (e.g.,

global climate change) are often filled with hyperbole and ideologically driven arguments. It is

my view that the quasi-experimental approach can produce evidence that can shift these debates

away from ideology and towards science. This might even produce more rational environmental

policies.

47

48

References The current draft does not contain all of the citations that it should. The next draft will have a fuller set of citations and the reference list will be more fully fleshed out. Altonji, Joseph G., Todd E. Elder, and Christopher R. Taber, “Selection on Observed and

Unobserved Variables: Assessing the Effectiveness of Catholic Schools,” NBER Working Paper No. 7831, 2000.

Angrist TK Angrist and Krueger JEP Angrist and Krueger Handbook of Labor Economics Chay, Kenneth. 1998, ILRR Chay, Kenneth and Michael Greenstone. 2001a. “The Impact of Air Pollution on Infant Mortality: Evidence from Geographic Variation in Pollution Shocks Induced by a Recession,” mimeograph, University of Chicago. Chay, Kenneth and Michael Greenstone. 2001b. “Air Quality, Infant Mortality, and the Clean Air Act of 1970,” (with Kenneth Chay), University of California, Berkeley, Center for Labor Economics Working Paper No. 42, August 2001. Cook, Thomas D. and Donald T. Campbell. 1979. Quasi-Experimentation: Design and Analysis Issues for Field Settings. Houghton Mifflin: Boston. Dockery et al. 1993. New England Journal of Medicine. Dockery, Douglas W., and C. Arden Pope, “Epidemiology of Acute Health Effects: Summary of

Time Series Studies.” in Richard Wilson and John Spengler, eds., Particles in Our Air (Cambridge, MA: Harvard University Press, 1996).

Freedman, David A. 1991. “Statistical Models and Shoe Leather,” Sociological Methodology, Vol. 21, pp 291-313. Fumento, Michael. 1997. Polluted Science: The EPA’s Campagign to Expand Clean Air Regualtions. Heckman TK Heckman and Vytlacil. 1999. “Instrumental Variables Methods for the Correlated Random Coefficient Model: Estimating the Average Rate of Return Schooling when the Return is Correlated with Schooling,” Journal of Human Resources, Vol. 33(4), pp. 974-87.

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Imbens, Guido W. and Joshua D. Angrist. 1994. “Identification and Estimation of Local Average Treatment Effects,” Econometrica, Vol. 62(2), 467-75. Per-Olov Johansson. 2001. “Is there a Meaningful Definition of the Value of a Statistical Life?” Journal of Health Economics, 2001 Lave, Lester B. and Eugene P. Seskin. 1970. “Air Pollution and Human Health.” Science. Remaining Information TK. Lave, Lester B. and Eugene P. Seskin. 1977. Air Pollution and Human Health. The Johns Hopkins University Press (for Resources for the Future): Baltimore. Meyer, Bruce D. “Natural and Quasi-Experiments in Economics.” 1994. NBER Technical Working Paper No. 170. Meyer, Bruce D. 1990. “Unemployment Insurance and Unemployment Spells,” Econometrica, 58: 757-82. Pope et al. 1995 Pope et al. 2002. Ransom, Michael R., and C. Arden Pope III, “External Health Costs of a Steel Mill,” Contemporary Economic Policy, VIII (1995), 86-97. Snow, John. (1855) 1965. On the Mode of Communication of Cholera. Reprent ed. New York: Hafner. Ashenfelter Lecture Karl Popper, Conjectures and Refutations, London: Routledge and Keagan Paul, 1963, pp. 33-39 from Theodore Shick, ed. Readings in the Philosophy of Science, Mountain View, CA: Mayfiedl Publishing Company, 2000, pp. 9-13. From The Weekly Standard on June 21, 1999, Wizards of Ozone, by Christopher DeMuth and Randall Lutter. Study: Pollution May Cause Asthma Illness Affects 9 Million U.S. Children By William Booth, Washington Post Staff Writer Friday, February 1, 2002; Page A02

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Table 1: Differences Across Counties by 1971 TSPs Levels

Variable Low TSPs

Concentration High TSPs

Concentration Probability

(1) = (2) (1) (2) (3) Infant Mortality Rate 1.72 1.85 .0002 TSPs Concentration µg/m3 60.3 106.12 .0001 County-Level Economic Variables Per Capita Income $11,135 $11,572 .0376 Employment/Population 44.8 48.4 .0246 Per Capita Public Assistance Medical Payments $74.2 $103.8

.0002

Per Capita Family Assistance $67.0 $99.5 .0001 Mean Parental Demographic and Socioeconomic Characteristics % Mother H.S. Dropout 18.7 18.8 .9390 Mother's Yrs Education 12.17 12.10 .3666 Father's Yrs Education 12.67 12.63 .6186 % Single Mother 7.2 8.7 .0677 % Black 12.8 19.5 .0001 Mean Medical Services Utilization % Zero Prenatal Care Visits 0.97 1.58 .0001 % Prenatal Care in 1st Trimester 58.2 55.0 .2124 Mean Maternal Health Endowment % Teenage Mother 16.3 17.7 .0018 % Mom >34 Years 5.66 5.86 .1504 % First Birth 37.1 37.4 .4562 % Prior Fetal Death 11.2 10.0 .0233 Mean Infant Health Endowment % Twins 1.80 1.86 .0969 Notes: The entries in columns (1) and (2) are the weighted means (where the weight is the total number of births) in counties that are below and above the median 1971 county-level TSPs concentration, respectively. Column (3) is the probability that the column (1) and (2) means are equal. The sample includes the 501 counties monitored for TSPs continuously from 1970 through 1972. See Chay and Greenstone (2002a) for more details.

Table 2: Cross-Sectional and Fixed Effects Estimates of the Association between Mean TSPs and Infant Mortality Rates Infant Deaths Due to Internal Causes (per 100,000 Live Births) (1) (2) (3) (4) (5) 1971 Cross-Section Mean TSPs 1.59 0.88 0.25 -0.05 1.06 (0.98) (0.51) (0.48) (0.44) (0.45) [501, .02] [495, .48] [482, .57] [460, .62] [482, .66] 1972 Cross-Section Mean TSPs 0.89 -0.30 -0.83 -1.32 -1.73 (1.20) (0.84) (0.74) (0.65) (0.82) [501, .00] [492, .33] [483, .43] [455, .48] [483, .53] 1971-1972 1st Differenced Mean TSPs 0.74 0.47 -0.14 -0.31 -0.54 (0.71) (0.71) (0.67) (0.67) (0.78) [501, .00] [489, .05] [474, .13] [449, .17] [474, .26] Basic Natality Vars. N Y Y Y Y Unrestricted Natality N N Y Y Y Income, Employment N N N Y N Income Assist. Sources N N N Y N Year Effects (Panels 1 and 2)

N N N N N

Year Effects (Panel 3) N N Y Y N State Fixed Effects N N N N Y Notes: The entries are the parameter estimates from the Mean TSPs variable and the associated standard errors from separate regressions. In any given year and specifications, the sample is further restricted to counties with nonmissing covariates. Standard errors are estimated using the Eicker-White formula to correct for heteroskedasticity and are reported in parentheses. Regressions are weighted by numbers of births in each county. The numbers in brackets are the number of counties and R-squareds of the regressions, respectively. The potential sample is limited to the 501 counties with TSPs data in 1970, 1971 and 1972. The infant mortality rate excludes deaths due to accidents, homicides and other “external” causes of death. The control variables are indicated in the row headings at the bottom of the table. The precise variables in each category are listed in the Data Appendix. State Fixed Effects are separate indicator variables for each state. Bold text indicates that the null hypothesis that the estimate is equal to zero can be rejected at the 5% level. See Chay and Greenstone (2002a) for more details.

Table 3: Instrumental Variables Estimates of the Effect of Mean TSPs on Infant Mortality Rates, Based on 1971-72 Changes Using 1972 Nonattainment Status as Instrument 1971-1972 Change in Infant Deaths (per 100,000 Live Births) (1) (2) (3) (4) (5) Mean TSPs 4.76 6.14 8.48 7.78 16.77 (1.57) (1.92) (4.12) (4.80) (7.09) County Effects Y Y Y Y Y Basic Natality Vars. N Y Y Y Y Unrestricted Natality N N Y Y Y Income, Employment N N N Y N Income Assist. Sources N N N Y N Year Effects N N Y Y N State-Year Effects N N N N Y Sample Size 501 489 474 449 474 Notes: Results are from two-stage least squares estimation using 1971-72 first-differences, with changes in mean TSPs instrumented by nonattainment status in 1972. Estimated standard errors allow for heteroskedasticity and are reported in parentheses. Regressions are weighted by numbers of births in each county and year.

Table 4: Instrumental Variables Estimates for Infant Deaths within 1-Year, For Counties with 1970 Geometric Mean TSPs near Regulatory Threshold (estimated standard errors in parentheses) 1971-72 Change in Infant Deaths Due to Internal Causes (per 100,000 Live Births) Geometric Mean of TSPs in the Regulation Selection Year in the Range of All Counties 30-150 µg/m3 50-100 µg/m3 60-90 µg/m3 65-85 µg/m3

(1) (2) (1) (2) (1) (2) (1) (2) (1) (2)

Mean TSPs 4.76 6.14 5.57 7.16 7.53 10.20 8.36 11.64 10.80 12.99 (1.57)

(1.92) (1.98) (2.11) (4.69) (4.62) (5.36) (5.71) (10.56) (10.32)

Basic Natality Vars.

N Y N Y N Y N Y N Y

Sample Size 501 489 435 428 279 276 176 173 120 117Notes: The dependent variables are the 1971-72 first-differences in the number of infant deaths due to internal causes within one-year, 28-days, and 24-hours of birth (per 100,000 live births). The columns correspond to subsamples of counties with annual geometric mean readings of TSPs in 1970 in the specified range. Results are from two-stage least squares estimation, with 1971-72 changes in mean TSPs instrumented by nonattainment status in 1972. Estimated standard errors allow for heteroskedasticity and are reported in parentheses. Regressions are weighted by numbers of births in each county and year.

Table 5: Summary Statistics of Hospital Admissions and Mortality Data for Utah and Cache Valleys with Utah Valley Steel Mill Open and Closed Utah Valley Cache Valley Average Daily Hospital Mill Mill Mill Mill Hospital Admissions Open Closed Open Closed Bronchitis and Asthma 0.925 0.737 0.220 0.237 (All Ages) (0.025) (0.045) (0.011) (0.026) Bronchitis and Asthma 0.322 0.152 0.079 0.073 (Preschool Ages) (0.014) (0.020) (0.007) (0.014) Pneumonia 1.237 1.010 0.534 0.376 (All Ages) (0.030) (0.056) (0.018) (0.030) Pneumonia 0.336 0.255 0.148 0.129 (Preschool Ages) (0.016) (0.027) (0.010) (0.018) Other Respiratory Diseases 0.837 0.586 0.322 0.280 (0.022) (0.039) (0.013) (0.027) Cardiovascular Diseases 3.964 3.904 1.509 1.505 (0.050) (0.110) (0.030) (0.069) Mortality 2.697 2.614 0.776 0.841 (0.048) (0.079) (0.025) (0.047) Population 1990 223,800 70,200 Notes: This table is an abridged version of Ransom and Pope’s (1995) Table 1.

Table 6: Estimates of Annual Excess Hospitalization Costs Associated with Operation of a Steel Mill in Utah Valley Difference-in-Differences Estimates Average Estimated Hospitalization Estimated Number Charge Per Total Excess Of Excess Admission Charges Admissions (1991$) (Thousands) (1) (2) (3) Bronchitis and Asthma 115.7 $4,030 $466 (All Ages) [20.2, 242.1] [$81, $975] Pneumonia -9.2 $7,725 -$71 (All Ages) [-79.7, 78.6] [-$615, $607] Other Respiratory Diseases 50.1 $6,167 $309 [-9.4, 126.9] [-$58, $783] Cardiovascular Diseases 138.2 $9,883 $1,366 [-39.9, 339.2] [-$394, $3,352] Total $2,070 [$90, $4050] Notes: This table is an abridged version of Ransom and Pope’s (1995) Table 3.

Figure 1: 1971-72 Post-Regulation Changes in Mean TSPs and Internal Infant Mortality Rates By Geometric Mean TSPs in Regulation Selection Year, 1970

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