[[pp. 5575-5624]] Diesel Particulate Matter Exposure of Underground Coal Miners

Note: EPA no longer updates this information, but it may be useful as a reference or resource.
 [Federal Register: January 19, 2001 (Volume 66, Number 13)]
[Rules and Regulations]
[Page 5575-5624]
From the Federal Register Online via GPO Access [wais.access.gpo.gov]
[DOCID:fr19ja01-12]

[[pp. 5575-5624]] Diesel Particulate Matter Exposure of Underground Coal Miners

[[Continued from page 5574]]

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m in diameter) are more strongly associated than ``coarse''
respirable particulates (i.e., particles greater than 2.5 m
but less than 10 m in diameter) with the adverse health
effects observed (EPA, 1996).
    MSHA recognizes that there are two difficulties involved in
utilizing the evidence from such studies in assessing risks to miners
from occupational dpm exposures. First, although dpm is a fine
particulate, ambient air also contains fine particulates other than
dpm. Therefore, health effects associated with exposures to fine
particulate matter in air pollution studies are not associated
specifically with exposures to dpm or any other one kind of fine
particulate matter. Second, observations of adverse health effects in
segments of the general population do not necessarily apply to the
population of miners. Since, due to age and selection factors, the
health of miners differs from that of the public as a whole, it is
possible that fine particles might not affect miners, as a group, to
the same degree as the general population.
    Some commenters reiterated these two points, recognized by MSHA in
the proposal, without addressing MSHA's stated reasons for including
health effects associated with fine particulates in this risk
assessment. There are compelling reasons why MSHA considered this body
of evidence in this rulemaking.
    Since dpm is a type of respirable particle, information about
health effects associated with exposures to respirable particles, and
especially to fine particulate matter, is certainly relevant, even if
difficult to apply directly to dpm exposures. Adverse health effects in
the general population have been observed at ambient atmospheric
particulate concentrations well below the dpm concentrations studied in
occupational settings. The potency of dpm differs from the total fine
particulate found in ambient air. This makes it difficult to establish
a specific exposure-response relationship for dpm that is based on fine
particle results. However, this does not mean that these results should
be ignored in a dpm risk assessment. The available evidence of adverse
health effects associated with fine particulates is still highly
relevant for dpm hazard identification. Furthermore, as shown in
Subsection 3.c.ii of this risk assessment, the fine particle research
findings can be used to construct a rough exposure-response
relationship for dpm, showing significantly increased risks of material
impairment among exposed miners. MSHA's estimates are based on the best
available epidemiologic evidence and show risks high enough to warrant
regulatory action.
    Moreover, extensive scientific literature shows that occupational
dust exposures contribute to the development of Chronic Obstructive
Pulmonary Diseases (COPD), thereby compromising the pulmonary reserve
of some miners. Miners experience COPD at a significantly higher rate
than the general population (Becklake 1989, 1992; Oxman 1993; NIOSH
1995). In addition, many miners also smoke tobacco. This places
affected miners in subpopulations specifically identified as
susceptible to the adverse health effects of respirable particle
pollution (EPA, 1996). Some commenters (e.g., MARG) repeated MSHA's
observation that the population of miners differs from the general
population but failed to address MSHA's concern for miners' increased
susceptibility due to COPD incidence and/or smoking habits. The Mine
Act requires that standards ``* * * most adequately assure on the basis
of the best available evidence that no miner suffer material impairment
of health or functional capacity * * *'' (Section 101(a)(6), emphasis
added). This most certainly authorizes MSHA to protect miners who have
COPD and/or smoke tobacco.
    MARG also submitted the opinion that if ``* * * regulation of fine
particulate matter is necessary, it [MSHA] should propose a rule
dealing specifically with the issue of concern, rather than a rule that
limits total airborne carbon or arbitrarily singles out diesel exhaust
* * *.'' MSHA's concern is not with ``total airborne carbon'' but with
dpm, which consists mostly of submicrometer airborne carbon. At issue
here, however, are the adverse health effects associated with dpm
exposure. Dpm is a type of fine particulate, and there is no evidence
to suggest that the dpm fraction contributes less than other fine
particulates to adverse health effects linked to exposures in ambient
air.
    For this reason, and because miners may be especially susceptible
to fine particle effects, MSHA has concluded, after considering the
public comments, that the body of evidence from air pollution studies
is highly relevant to this risk assessment. The Agency is, therefore,
taking the evidence fully into account.
b. Acute Health Effects
    Information pertaining to the acute health effects of dpm includes
anecdotal reports of symptoms experienced by exposed miners, studies
based on exposures to diesel emissions, and studies based on exposures
to particulate matter in the ambient air. These will be discussed in
turn. Subsection 2.a.iii of this risk assessment addressed the
relevance to dpm of studies based on exposures to particulate matter in
the ambient air.
    Only the evidence from human studies will be addressed in this
section. Data from genotoxicity studies and studies on laboratory
animals will be discussed later, in Subsection 2.d on mechanisms of
toxicity. Section 3.a and 3.b contain MSHA's interpretation of the
evidence relating dpm exposures to acute health hazards.
i. Symptoms Reported by Exposed Miners
    Miners working in mines with diesel equipment have long reported
adverse effects after exposure to diesel exhaust. For example, at the
dpm workshops conducted in 1995, a miner reported headaches and nausea
experienced by several operators after short periods of exposure (dpm
Workshop; Mt. Vernon, IL, 1995). Another miner reported that smoke from
poorly maintained equipment, or from improper fuel use, irritates the
eyes, nose, and throat. ``We've had people sick time and time again * *
* at times we've had to use oxygen for people to get them to come back
around to where they can feel normal again.'' (dpm Workshop; Beckley,
WV, 1995). Other miners (dpm Workshops; Beckley, WV, 1995; Salt Lake
City, UT, 1995), reported similar symptoms in the various mines where
they worked.
    At the 1998 public hearings on MSHA's proposed dpm rule for coal
mines, one miner, with work experience in a coal mine utilizing diesel
haulage equipment at the face, testified that

    * * * unlike many, I have not experienced the headaches, the
watering of the eyes, the cold-like symptoms and walking around in
this cloud of smoke. Maybe it's because of the maintenance programs.
Maybe it's because of complying with ventilation. * * * after 25
years, I have not shown any effects. [SLC, 1998]

    Other miners working at dieselized coal mines testified at those
hearings that they had personally experienced eye irritation and/or
respiratory ailments immediately after exposure to diesel exhaust, and
they attributed these ailments to their exposure. For example, one
miner attributed a case of pneumonia to a specific episode of unusually
high exposure. (Birm., 1998) The safety and training manager of the
mining company involved noted that ``there had been a problem
recognized in review with that exhaust system on that particular piece
of equipment'' and that the pneumonia may have

[[Page 5576]]

developed due to ``idiosyncracy of his lungs that respond to any type
of a respiratory irritant.'' The manager suggested that this incident
should not be generalized to other situations but provided no evidence
that the miner's lungs were unusually susceptible to irritation.\21\
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    \21\ MSHA realizes the incidents related in this subsection are
anecdotal and draws no statistical conclusions from them. Since they
pertain to specific experiences, however, they can be useful in
identifying a potential hazard.
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    Another miner, who had worked at the same underground mine before
and after diesel haulage equipment was introduced, indicated that he
and his co-workers began experiencing acute symptoms after the diesel
equipment was introduced. This miner suggested that these effects were
linked to exposure, and referring to a co-worker stated:

    * * * had respiratory problems, after * * * diesel equipment was
brought into that mine--he can take off for two weeks vacation, come
back--after that two weeks, he felt pretty good, his respiratory
problems would straighten up, but at the very instant that he gets
back in the face of diesel-powered equipment, it starts up again,
his respiratory problems will flare up again, coughing, sore throat,
numerous problems in his chest. (Birm., 1998).

    Several other underground miners asserted there was a correlation
between diesel exposure levels and the frequency and/or intensity of
respiratory symptoms, eye irritations, and chest ailments. One miner,
for example, stated:

    I've experienced [these symptoms] myself. * * * other miners
experience the same kind of distresses * * * Some of the stresses
you actually can feel--you don't need a gauge to measure this--your
burning eyes, nose, throat, your chest irritation. The more you're
exposed to, the higher this goes. This includes headaches and nausea
and some lasting congestion, depending on how long you've been
exposed per shift or per week.
    The men I represent have experienced more cold-like symptoms,
especially over the past, I would say, eight to ten years, when
diesel has really peaked and we no longer really use much of
anything else. [SLC, 1998]

    Kahn et al. (1988) conducted a study of the prevalence and
seriousness of such complaints, based on United Mine Workers of America
records and subsequent interviews with the miners involved. The review
involved reports at five underground coal mines in Utah and Colorado
between 1974 and 1985. Of the 13 miners reporting symptoms: 12 reported
mucous membrane irritation, headache and light-headiness; eight
reported nausea; four reported heartburn; three reported vomiting and
weakness, numbness, and tingling in extremities; two reported chest
tightness; and two reported wheezing (although one of these complained
of recurrent wheezing without exposure). All of these incidents were
severe enough to result in lost work time due to the symptoms (which
subsided within 24 to 48 hours).
    In comments submitted for this rulemaking, the NMA pointed out, as
has MSHA, that the evidence presented in this subsection is anecdotal.
The NMA, further, suggested that the cited article by Kahn et al.
typified this kind of evidence in that it was ``totally devoid of any
correlation to actual exposure levels.'' A lack of concurrent exposure
measurements is, unfortunately, not restricted to anecdotal evidence;
and MSHA must base its evaluation on the available evidence. MSHA
recognizes the scientific limitations of anecdotal evidence and has,
therefore, compiled and considered it separately from more formal
evidence. MSHA nevertheless considers such evidence potentially
valuable for identifying acute health hazards, with the understanding
that confirmation requires more rigorous investigation.\22\
    With respect to the same article (Kahn et al., 1988), and
notwithstanding the NMA's claim that the article was totally devoid of
any correlation to exposure levels, the NMA also stated that MSHA:

    * * * neglects to include in the preamble the article's
description of the conditions under which the ``overexposures''
occurred, e.g., ``poor engine maintenance, poor maintenance of
emission controls, prolonged idling of machinery, engines pulling
heavy loads, use of equipment during times when ventilation was
disrupted (such as during a move of longwall machinery), use of
several pieces of equipment exhausting into the fresh-air intake,
and use of poor quality fuel.
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    \22\ MSHA sees potential value in anecdotal evidence when it
relates to immediate experiences. MSHA regards anecdotal evidence to
be less appropriate for identifying chronic health effects, since
chronic effects cannot readily be linked to specific experiences.
Accordingly, this risk assessment places little weight on anecdotal
evidence for the chronic health hazards considered.
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The NMA asserted that these conditions, cited in the article, ``have
been addressed by MSHA's final standards for diesel equipment in
underground coal mines issued October 25, 1996.''\23\ Furthermore,
despite its reservations about anecdotal evidence:
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    \23\ The 1996 regulations to which the NMA was referring do not
apply to M/NM mines.

    NMA is mindful of the testimony of several miners in the coal
proceeding who complained of transient irritation owing to exposure
to diesel exhaust. * * * the October 1996 regulations together with
the phased-in introduction of catalytic converters on all outby
equipment and the introduction of such devices on permissible
equipment when such technology becomes available will address the
---------------------------------------------------------------------------
complaints raised by the miners.

    The NMA provided no evidence, however, that elimination of the
conditions described by Kahn et al., or implementation of the 1996
diesel regulations for coal mines, would reduce dpm levels sufficiently
to prevent the sensory irritations and respiratory symptoms described.
MSHA completed an analysis of the impact of the 1996 diesel regulations
for underground coal mines (See Part II, Section 7). We do expect that
the concentrations of diesel emissions at the section loading point and
during longwall moves will be reduced as these provisions are fully
implemented. These dpm levels, though reduced, are still above the
exposures expected to cause sensory irritations and respiratory
symptoms (See Section 3(d)(5)). MSHA did not explicitly consider the
risks to miners of a working lifetime of dpm exposure at very high
levels, nor the actions that could be taken to specifically reduce dpm
exposure levels in underground coal mines when developing the 1996
underground coal diesel regulations. It was understood that the agency
would be taking a separate look at the health risks of dpm exposure. In
addition, the NMA did not provide evidence that these are the only
conditions under which complaints of sensory irritations and
respiratory symptoms occur, or explain why eliminating them would
reduce the need to prevent excessive exposures under other conditions.
    In the proposal for the present rule, MSHA requested additional
information about such effects from medical personnel who have treated
miners. IMC Global submitted letters from four healthcare practitioners
in Carlsbad, NM, including three physicians. None of these
practitioners attributed any cases of respiratory problems or other
acute symptoms to dpm exposure. Three of the four practitioners noted
that they had observed respiratory symptoms among exposed miners but
attributed these symptoms to chronic lung conditions, smoking, or other
factors. One physician stated that ``[IMC Global], which has used
diesel equipment in its mining operations for over 20 years, has never
experienced a single case of injury or illness caused by exposures to
diesel particulates.''
ii. Studies Based on Exposures to Diesel Emissions
    Several experimental and statistical studies have been conducted to
investigate acute effects of exposure to

[[Page 5577]]

diesel emissions. These more formal studies provide data that are more
scientifically rigorous than the anecdotal evidence presented in the
preceding subsection. Unless otherwise indicated, diesel exhaust
exposures were determined qualitatively.
    In a clinical study (Battigelli, 1965), volunteers were exposed to
three concentrations of diluted diesel exhaust and then evaluated to
determine the effects of exposure on pulmonary resistance and the
degree of eye irritation. The investigators stated that ``levels
utilized for these controlled exposures are comparable to realistic
values such as those found in railroad shops.'' No statistically
significant change in pulmonary function was detected, but exposure for
ten minutes to diesel exhaust diluted to the middle level produced
``intolerable'' irritation in some subjects while the average
irritation score was midway between ``some'' irritation and a
``conspicuous but tolerable'' irritation level. Diluting the
concentration by 50% substantially reduced the irritation. At the
highest exposure level, more than 50 percent of the volunteers
discontinued the experiment before 10 minutes because of
``intolerable'' eye irritation.
    A study of underground iron ore miners exposed to diesel emissions
found no difference in spirometry measurements taken before and after a
work shift (Jorgensen and Svensson 1970). Similarly, another study of
coal miners exposed to diesel emissions detected no statistically
significant relationship between exposure and changes in pulmonary
function (Ames et al. 1982). However, the authors noted that the lack
of a statistically significant result might be due to the low
concentrations of diesel emissions involved.
    Gamble et al. (1978) observed decreases in pulmonary function over
a single shift in salt miners exposed to diesel emissions. Pulmonary
function appeared to deteriorate in relation to the concentration of
diesel exhaust, as indicated by NO2; but this effect was
confounded by the presence of NO2 due to the use of
explosives.
    Gamble et al. (1987a) assessed response to diesel exposure among
232 bus garage workers by means of a questionnaire and before- and
after-shift spirometry. No significant relationship was detected
between diesel exposure and change in pulmonary function. However,
after adjusting for age and smoking status, a significantly elevated
prevalence of reported symptoms was found in the high-exposure group.
The strongest associations with exposure were found for eye irritation,
labored breathing, chest tightness, and wheeze. The questionnaire was
also used to compare various acute symptoms reported by the garage
workers and a similar population of workers at a lead acid battery
plant who were not exposed to diesel fumes. The prevalence of work-
related eye irritations, headaches, difficult or labored breathing,
nausea, and wheeze was significantly higher in the diesel bus garage
workers, but the prevalence of work-related sneezing was significantly
lower.
    Ulfvarson et al. (1987) studied effects over a single shift on 47
stevedores exposed to dpm at particle concentrations ranging from 130
/m\3\ to 1000 /m\3\. Diesel particulate
concentrations were determined by collecting particles on glass fiber
filters of unspecified efficiency. A statistically significant loss of
pulmonary function was observed, with recovery after 3 days of no
occupational exposure.
    To investigate whether removal of the particles from diesel exhaust
might reduce the ``acute irritative effect on the lungs'' observed in
their earlier study, Ulfvarson and Alexandersson (1990) compared
pulmonary effects in a group of 24 stevedores exposed to unfiltered
diesel exhaust to a group of 18 stevedores exposed to filtered exhaust,
and to a control group of 17 occupationally unexposed workers. The
filters used were specially constructed from 144 layers of glass fiber
with ``99.97% degrees of retention of dioctylphthalate mist with
particle size 0.3 m.'' Workers in all three groups were
nonsmokers and had normal spirometry values, adjusted for sex, age, and
height, prior to the experimental workshift.
    In addition to confirming the earlier observation of significantly
reduced pulmonary function after a single shift of occupational
exposure, the study found that the stevedores in the group exposed only
to filtered exhaust had 50-60% less of a decline in forced vital
capacity (FVC) than did those stevedores who worked with unfiltered
equipment. Similar results were observed for a subgroup of six
stevedores who were exposed to filtered exhaust on one shift and
unfiltered exhaust on another. No loss of pulmonary function was
observed for the unexposed control group. The authors suggested that
these results ``support the idea that the irritative effect of diesel
exhausts [sic] to the lungs is the result of an interaction between
particles and gaseous components and not of the gaseous components
alone.'' They concluded that ``* * * it should be a useful practice to
filter off particles from diesel exhausts in work places even if
potentially irritant gases remain in the emissions'' and that ``removal
of the particulate fraction by filtering is an important factor in
reducing the adverse effect of diesel exhaust on pulmonary function.''
    Rudell et al. (1996) carried out a series of double-blind
experiments on 12 healthy, non-smoking subjects to investigate whether
a particle trap on the tailpipe of an idling diesel engine would reduce
acute effects of diesel exhaust, compared with exposure to unfiltered
exhaust. Symptoms associated with exposure included headache,
dizziness, nausea, tiredness, tightness of chest, coughing, and
difficulty in breathing. The most prominent symptoms were found to be
irritation of the eyes and nose, and a sensation of unpleasant smell.
Among the various pulmonary function tests performed, exposure was
found to result in significant changes only as measured by increased
airway resistance and specific airway resistance. The ceramic wall flow
particle trap reduced the number of particles by 46 percent, but
resulted in no significant attenuation of symptoms or lung function
effects. The authors concluded that diluted diesel exhaust caused
increased irritant symptoms of the eyes and nose, unpleasant smell, and
bronchoconstriction, but that the 46-percent reduction in median
particle number concentration observed was not sufficient to protect
against these effects in the populations studied.
    Wade and Newman (1993) documented three cases in which railroad
workers developed persistent asthma following exposure to diesel
emissions while riding immediately behind the lead engines of trains
having no caboose. None of these workers were smokers or had any prior
history of asthma or other respiratory disease. Asthma diagnosis was
based on symptoms, pulmonary function tests, and measurement of airway
hyperreactivity to methacholine or exercise.
    Although MSHA is not aware of any other published report directly
relating diesel emissions exposures to the development of asthma, there
have been a number of recent studies indicating that dpm exposure can
induce bronchial inflammation and respiratory immunological allergic
responses in humans. Studies published through 1997 are reviewed in
Peterson and Saxon (1996) and Diaz-Sanchez (1997).
    Diaz-Sanchez et al. (1994) challenged healthy human volunteers by
spraying

[[Page 5578]]

300 g dpm into their nostrils.\24\ Immunoglobulin E (IgE)
binds to mast cells where it binds antigen leading to secretion of
biologically active amines (e.g., histamine) causing dilation and
increased permeability of blood vessels. These amines are largely
responsible for clinical manifestations of such allergic reactions as
hay fever, asthma, and hives. Enhanced IgE levels were found in nasal
washes in as little as 24 hours, with peak production observed 4 days
after the dpm was administered.\25\ No effect was observed on the
levels of other immunoglobulin proteins. The selective enhancement of
local IgE production was demonstrated by a dramatic increase in IgE-
secreting cells. The authors suggested that dpm may augment human
allergic disease responses by enhancing the production of IgE
antibodies. Building on these results, Diaz-Sanchez et al. (1996)
measured cytokine production in nasal lavage cells from healthy human
volunteers challenged with 150 g dpm sprayed into each
nostril. Based on the responses observed, including a broad increase in
cytokine production, along with the results of the 1994 paper, the
authors concluded that dpm exposure contributes to enhanced local IgE
production and thus plays a role in allergic airway disease.
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    \24\ Assuming that a working miner inhales approximately 1.25
m\3\ of air per hour, this dose corresponds to a 1-hour exposure at
a dpm concentration of 240 g/m\3\.
    \25\ IgE is one of five types of immunoglobulin, which are
proteins produced in response to allergens. Cytokine (mentioned
later) is a substance involved in regulating IgE production.
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    Salvi et al. (1999) exposed healthy human volunteers to diluted
diesel exhaust at a dpm concentration of 300 g/m\3\ for one
hour with intermittent exercise. Although there were no changes in
pulmonary function, there were significant increases in various markers
of allergic response in airway lavage fluid. Bronchial biopsies
obtained six hours after exposure also showed significant increases in
markers of immunologic response in the bronchial tissue. Significant
increases in other markers of immunologic response were also observed
in peripheral blood following exposure. A marked cellular inflammatory
response in the airways was reported. The authors concluded that ``at
high ambient concentrations, acute short-term DE [diesel exhaust]
exposure produces a well-defined and marked systemic and pulmonary
inflammatory response in healthy human volunteers, which is
underestimated by standard lung function measurements.''
iii. Studies Based on Exposures to Particulate Matter in Ambient Air
    Due to an incident in Belgium's industrial Meuse Valley, it was
known as early as the 1930s that large increases in particulate air
pollution, created by winter weather inversions, could be associated
with large simultaneous increases in mortality and morbidity. More than
60 persons died from this incident, and several hundred suffered
respiratory problems. The mortality rate during the episode was more
than ten times higher than normal, and it was estimated that over 3,000
sudden deaths would occur if a similar incident occurred in London.
Although no measurements of pollutants in the ambient air during the
episode are available, high PM levels were obviously present (EPA,
1996).
    A significant elevation in particulate matter (along with
SO2 and its oxidation products) was measured during a 1948
incident in Donora, PA. Of the Donora population, 42.7 percent
experienced some acute adverse health effect, mainly due to irritation
of the respiratory tract. Twelve percent of the population reported
difficulty in breathing, with a steep rise in frequency as age
progressed to 55 years (Schrenk, 1949).
    Approximately as projected by Firket (1931), an estimated 4,000
deaths occurred in response to a 1952 episode of extreme air pollution
in London. The nature of these deaths is unknown, but there is clear
evidence that bronchial irritation, dyspnea, bronchospasm, and, in some
cases, cyanosis occurred with unusual prevalence (Martin, 1964).
    These three episodes ``left little doubt about causality in regard
to the induction of serious health effects by very high concentrations
of particle-laden air pollutant mixtures'' and stimulated additional
research to characterize exposure-response relationships (EPA, 1996).
Based on several analyses of the 1952 London data, along with several
additional acute exposure mortality analyses of London data covering
later time periods, the U.S. Environmental Protection Agency (EPA)
concluded that increased risk of mortality is associated with exposure
to combined particulate and SO2 levels in the range of 500-
1000 g/m3. The EPA also concluded that relatively
small, but statistically significant increases in mortality risk exist
at particulate (but not SO2) levels below 500 g/
m3, with no indications of a specific threshold level yet
indicated at lower concentrations (EPA, 1986).
    Subsequently, between 1986 and 1996, increasingly sophisticated
techniques of particulate measurement and statistical analysis have
enabled investigators to address these questions more quantitatively.
The studies on acute effects carried out since 1986 are reviewed in the
1996 EPA Air Quality Criteria for Particulate Matter, which forms the
basis for the discussion below (EPA, 1996).
    At least 21 studies have been conducted that evaluate associations
between acute mortality and morbidity effects and various measures of
fine particulate levels in the ambient air. These studies are
identified in Tables III-2 and III-3. Table III-2 lists 11 studies that
measured primarily fine particulate matter using filter-based optical
techniques and, therefore, provide mainly qualitative support for
associating observed effects with fine particles. Table III-3 lists
quantitative results from 10 studies that reported gravimetric
measurements of either the fine particulate fraction or of components,
such as sulfates, that serve as indicators or surrogates of fine
particulate exposures.

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    A total of 38 studies examining relationships between short-term
particulate levels and increased mortality, including nine with fine
particulate measurements, were published between 1988 and 1996 (EPA,
1996). Most of these found statistically significant positive
associations. Daily or several-day elevations of particulate
concentrations, at average levels as low as 18-58 g/
m3, were associated with increased mortality, with stronger
relationships observed in those with preexisting respiratory and
cardiovascular disease. Overall, these studies suggest that an increase
of 50 g/m3 in the 24-hour average of
PM10 is associated with a 2.5 to 5-percent increase in the
risk of mortality in the general population, excluding accidents,
suicides, and homicides. Based on Schwartz et al. (1996), the relative
risk of mortality in the general population increases by about 2.6 to
5.5 percent per 25 g/m3 of fine particulate
(PM2.5) (EPA, 1996). More specifically, Schwartz et al.
(1996) reported significantly elevated risks of mortality due to
pneumonia, chronic obstructive pulmonary disease (COPD), and ischemic
heart disease (IHD). For these three causes of death, the estimated
increases in risk per incremental increase of 10 g/
m3 in the concentration of PM2.5 were 4.0
percent, 3.3 percent, and 2.1 percent, respectively. Each of these
three results was statistically significant at a 95-percent confidence
level.
    A total of 22 studies were published on associations between short-
term particulate levels and hospital admissions, outpatient visits, and
emergency room visits for respiratory disease, Chronic Obstructive
Pulmonary Disease (COPD), pneumonia, and heart disease (EPA, 1996).
Fifteen of these studies were focused on the elderly. Of the seven that
dealt with all ages (or in one case, persons less than 65 years old),
all showed positive results. All of the five studies relating fine
particulate measurements to increased hospitalization, listed in Tables
III-2 and III-3, dealt with general age populations and showed
statistically significant associations. The estimated increase in risk
ranges from 3 to 16 percent per 25 g/m3 of fine
particulate. Overall, these studies are indicative of acute morbidity
effects being related to fine particulate matter and support the
mortality findings.
    Most of the 14 published quantitative studies on ambient
particulate exposures and acute respiratory diseases were restricted to
children (EPA, 1996, Table 12-12). Although they generally showed
positive associations, and may be of considerable biological relevance,
evidence of toxicity in children is not necessarily applicable to
adults. The few studies on adults have not produced statistically
significant evidence of a relationship.
    Thirteen studies since 1982 have investigated associations between
ambient particulate levels and loss of pulmonary function (EPA, 1996,
Table 12-13). In general, these studies suggest a short term effect,
especially in symptomatic groups such as asthmatics, but most were
carried out on children only. In a study of adults with mild COPD, Pope
and Kanner (1993) found a 29  10 ml decrease in 1-second
Forced Expiratory Volume (FEV1) per 50 g/
m3 increase in PM10, which is similar in
magnitude to the change generally observed in the studies on children.
In another study of adults, with PM10 ranging from 4 to 137
g/m3, Dusseldorp et al. (1995) found 45 and 77 ml/
sec decreases, respectively, for evening and morning Peak Expiratory
Flow Rate (PEFR) per 50 g/m3 increase in
PM10 (EPA, 1996). In the only study carried out on adults
that specifically measured fine particulate (PM2.5), Perry
et al. (1983) did not detect any association of exposure with loss of
pulmonary function. This study, however, was conducted on only 24
adults (all asthmatics) exposed at relatively low concentrations of
PM2.5 and, therefore, had very little power to detect any
such association.
c. Chronic Health Effects
    During the 1995 dpm workshops, miners reported observable adverse
health effects among those who have worked a long time in dieselized
mines. For example, a miner (dpm Workshop; Salt Lake City, UT, 1995),
stated that miners who work with diesel ``have spit up black stuff
every night, big black--what they call black (expletive) * * * [they]
have the congestion every night * * * the 60-year-old man working there
40 years.'' Similarly, in comments submitted in response to MSHA's
proposed dpm regulations, several miners reported cancers and chronic
respiratory ailments they attributed to dpm exposure.
    Scientific investigation of the chronic health effects of dpm
exposure includes studies based specifically on exposures to diesel
emissions and studies based more generally on exposures to fine
particulate matter in the ambient air. Only the evidence from human
studies will be addressed in this section of the risk assessment. Data
from genotoxicity studies and studies on laboratory animals will be
discussed later, in Subsection 2.d on mechanisms of toxicity.
Subsection 3.a(iii) contains MSHA's interpretation of the evidence
relating dpm exposures to one chronic health hazard: lung cancer.
i. Studies Based on Exposures to Diesel Emissions
    The discussion will (1) summarize the epidemiologic literature on
chronic effects other than cancer, and then (2) concentrate on the
epidemiology of cancer in workers exposed to dpm.
(1) Chronic Effects Other Than Cancer
    A number of epidemiologic studies have investigated relationships
between diesel exposure and the risk of developing persistent
respiratory symptoms (i.e., chronic cough, chronic phlegm, and
breathlessness) or measurable loss in lung function. Three studies
involved coal miners (Reger et al., 1982; Ames et al., 1984; Jacobsen
et al., 1988); four studies involved metal and nonmetal miners
(Jorgenson & Svensson, 1970; Attfield, 1979; Attfield et al., 1982;
Gamble et al., 1983). Three studies involved other groups of workers--
railroad workers (Battigelli et al., 1964), bus garage workers (Gamble
et al., 1987), and stevedores (Purdham et al., 1987).
    Reger et al. (1982) examined the prevalence of respiratory symptoms
and the level of pulmonary function among more than 1,600 underground
and surface U.S. coal miners, comparing results for workers (matched
for smoking status, age, height, and years worked underground) at
diesel and non-diesel mines. Those working at underground dieselized
mines showed some increased respiratory symptoms and reduced lung
function, but a similar pattern was found in surface miners who
presumably would have experienced less diesel exposure. Miners in the
dieselized mines, however, had worked underground for less than 5 years
on average.
    In a study of 1,118 U.S. coal miners, Ames et al. (1984) did not
detect any pattern of chronic respiratory effects associated with
exposure to diesel emissions. The analysis, however, took no account of
baseline differences in lung function or symptom prevalence, and the
authors noted a low level of exposure to diesel-exhaust contaminants in
the exposed population.
    In a cohort of 19,901 British coal miners investigated over a 5-
year period, Jacobsen et al. (1988) found increased work absence due to
self-reported chest illness in underground workers exposed to diesel
exhaust, as compared to surface workers, but found

[[Page 5582]]

no correlation with their estimated level of exposure.
    Jorgenson & Svensson (1970) found higher rates of chronic
productive bronchitis, for both smokers and nonsmokers, among Swedish
underground iron ore miners exposed to diesel exhaust as compared to
surface workers at the same mine. No significant difference was found
in spirometry results.
    Using questionnaires collected from 4,924 miners at 21 U.S. metal
and nonmetal mines, Attfield (1979) evaluated the effects of exposure
to silica dust and diesel exhaust and obtained inconclusive results
with respect to diesel exposure. For both smokers and non-smokers,
miners occupationally exposed to diesel for five or more years showed
an elevated prevalence of persistent cough, persistent phlegm, and
shortness of breath, as compared to miners exposed for less than five
years, but the differences were not statistically significant. Four
quantitative indicators of diesel use failed to show consistent trends
with symptoms and lung function.
    Attfield et al. (1982) reported on a medical surveillance study of
630 white male miners at 6 U.S. potash mines. No relationships were
found between measures of diesel use or exposure and various health
indices, based on self-reported respiratory symptoms, chest
radiographs, and spirometry.
    In a study of U.S. salt miners, Gamble and Jones (1983) observed
some elevation in cough, phlegm, and dyspnea associated with mines
ranked according to level of diesel exhaust exposure. No association
between respiratory symptoms and estimated cumulative diesel exposure
was found after adjusting for differences among mines. However, since
the mines varied widely with respect to diesel exposure levels, this
adjustment may have masked a relationship.
    Battigelli et al. (1964) compared pulmonary function and complaints
of respiratory symptoms in 210 U.S. railroad repair shop employees,
exposed to diesel for an average of 10 years, to a control group of 154
unexposed railroad workers. Respiratory symptoms were less prevalent in
the exposed group, and there was no difference in pulmonary function;
but no adjustment was made for differences in smoking habits.
    In a study of workers at four diesel bus garages in two U.S.
cities, Gamble et al. (1987b) investigated relationships between job
tenure (as a surrogate for cumulative exposure) and respiratory
symptoms, chest radiographs, and pulmonary function. The study
population was also compared to an unexposed control group of workers
with similar socioeconomic background. After indirect adjustment for
age, race, and smoking, the exposed workers showed an increased
prevalence of cough, phlegm, and wheezing, but no association was found
with job tenure. Age- and height-adjusted pulmonary function was found
to decline with duration of exposure, but was elevated on average, as
compared to the control group. The number of positive radiographs was
too small to support any conclusions. The authors concluded that the
exposed workers may have experienced some chronic respiratory effects.
    Purdham et al. (1987) compared baseline pulmonary function and
respiratory symptoms in 17 exposed Canadian stevedores to a control
group of 11 port office workers. After adjustment for smoking, there
was no statistically significant difference in self-reported
respiratory symptoms between the two groups. However, after adjustment
for smoking, age, and height, exposed workers showed lower baseline
pulmonary function, consistent with an obstructive ventilatory defect,
as compared to both the control group and the general metropolitan
population.
    In a review of these studies, Cohen and Higgins (1995) concluded
that they did not provide strong or consistent evidence for chronic,
nonmalignant respiratory effects associated with occupational exposure
to diesel exhaust. These reviewers stated, however, that ``several
studies are suggestive of such effects * * * particularly when viewed
in the context of possible biases in study design and analysis.'' Glenn
et al (1983) noted that the studies of chronic respiratory effects
carried out by NIOSH researchers in coal, salt, potash, and trona mines
all ``revealed an excess of cough and phlegm in the diesel exposed
group.'' IPCS (1996) noted that ``[a]lthough excess respiratory
symptoms and reduced pulmonary function have been reported in some
studies, it is not clear whether these are long-term effects of
exposure.'' Similarly, Morgan et al. (1997) concluded that while there
is ``some evidence that the chronic inhalation of diesel fumes leads to
the development of cough and sputum, that is chronic bronchitis, it is
usually impossible to show a cause and effect relationship * * *.''
MSHA agrees that these dpm studies are not conclusive but considers
them to be suggestive of adverse chronic, non-cancerous respiratory
effects.
(2) Cancer
    Because diesel exhaust has long been known to contain carcinogenic
compounds (e.g., benzene in the gaseous fraction and benzopyrene and
nitropyrene in the dpm fraction), a great deal of research has been
conducted to determine if occupational exposure to diesel exhaust
actually results in an increased risk of cancer. Evidence that exposure
to dpm increases the risk of developing cancer comes from three kinds
of studies: human studies, genotoxicity studies, and animal studies. In
this risk assessment, MSHA has placed the most weight on evidence from
the human epidemiologic studies and views the genotoxicity and animal
studies as lending support to the epidemiologic evidence.
    In the epidemiologic studies, it is generally impossible to
disassociate exposure to dpm from exposure to the gasses and vapors
that form the remainder of whole diesel exhaust. However, the animal
evidence shows no significant increase in the risk of lung cancer from
exposure to the gaseous fraction alone (Heinrich et al., 1986, 1995;
Iwai et al., 1986; Brightwell et al., 1986). Therefore, dpm, rather
than the gaseous fraction of diesel exhaust, is usually assumed to be
the agent associated with any excess prevalence of lung cancer observed
in the epidemiologic studies. Subsection 2.d of this risk assessment
contains a summary of evidence supporting this assumption.
(a) Lung Cancer
    MSHA evaluated 47 epidemiologic studies examining the prevalence of
lung cancer within groups of workers occupationally exposed to dpm.
This includes four studies not included in MSHA's risk assessment as
originally proposed.\26\ The earliest of these studies was published in
1957 and the latest in 1999. The most recent published reviews of these
studies are by Mauderly (1992), Cohen and Higgins (1995), Muscat and
Wynder (1995), IPCS (1996), Stober and Abel (1996), Cox (1997), Morgan
et al. (1997), Cal-EPA (1998), ACGIH (1998), and U.S. EPA (1999). In
response to both the ANPRM and the 1998 proposals, several commenters
also provided MSHA with

[[Page 5583]]

their own reviews of many of these studies. In arriving at its
conclusions, MSHA considered all of these reviews, including those of
the commenters, as well as the 47 source studies available to MSHA.
---------------------------------------------------------------------------

    \26\ One of these studies (Christie et al., 1995) was cited in
the discussion on mechanisms of toxicity but not considered in
connection with studies involving dpm exposures. Several commenters
advocated that it be considered. The other three were published in
1997 or later. Johnston et al. (1997) was introduced to these
proceedings in 64 FR 7144. Saverin et al. (1999) is the published
English version of a Germany study submitted as part of the public
comments by NIOSH on May 27, 1999. The remaining study is Bruske-
Hohlfeld et al. (1999).
---------------------------------------------------------------------------

    In addition, MSHA relied on two comprehensive statistical ``meta-
analyses'' \27\ of the epidemiologic literature: Lipsett and Campleman
(1999) thru \28\ and Bhatia et al. (1998).\29\ These meta-analyses,
which weight, combine, and analyze data from the various epidemiologic
studies, were themselves the subject of considerable public comment and
are discussed primarily in Subsection 3.a.iii of this risk assessment.
The present section tabulates results of the studies and addresses
their individual strengths and weaknesses. Interpretation and
evaluation of the collective evidence, including discussion of
potential publication bias or any other systematic biases, is deferred
to Subsection 3.a.iii.
---------------------------------------------------------------------------

    \27\ MSHA restricts the term ``meta-analysis'' to formal,
statistical analyses of the pooled data taken from several studies.
Some commenters (and Cox in the article itself) referred to the
review by Cox (op.cit.) as a meta-analysis. Although this article
seeks to identify characteristics of the individual studies that
might account for the general pattern of results, it performs no
statistical analysis on the pooled epidemiologic data. For this
reason, MSHA does not regard the Cox article as a meta-analysis in
the same sense as the two studies so identified. MSHA does, however,
recognize that the Cox article evaluates and rejects the collective
evidence for causality, based on the common characteristics
identified. In that context, Cox's arguments and conclusions are
addressed in Subsection 3.a.iii. Cox also presents a statistical
analysis of data from one of the studies, and that portion of the
article is considered here, along with his observations about other
individual studies.
    \28\ MSHA's risk assessment as originally proposed cited an
unpublished version, attributed to Lipsett and Alexexeff (1998), of
essentially the same meta-analysis. Both the 1999 and 1998 versions
are now in the public record.
    \29\ Silverman (1998) reviewed the meta-analysis by Bhatia et
al. (op cit.) and discussed, in general terms, the body of available
epidemiologic evidence on which it is based. Some commenters stated
that MSHA had not sufficiently considered Silverman's views on the
limitations of this evidence. MSHA has thoroughly considered these
views and addresses them in Subsection 3.a.(iii).
---------------------------------------------------------------------------

    Tables III-4 (27 cohort studies) and III-5 (20 case-control
studies) identify all 47 known epidemiologic studies that MSHA
considers relevant to an assessment of lung cancer risk associated with
dpm exposure.\30\ These tables include, for each of the 47 studies
listed, a brief description of the study and its findings, the method
of exposure assessment, and comments on potential biases or other
limitations. Presence or absence of an adjustment for smoking habits is
highlighted, and adjustments for other potentially confounding factors
are indicated when applicable. Although MSHA constructed these tables
based primarily on its own reading of the 48 source publications, the
tables also incorporate strengths and weaknesses noted in the
literature reviews and/or in the public comments submitted.
---------------------------------------------------------------------------

    \30\ For simplicity, the epidemiologic studies considered here
are placed into two broad categories. A cohort study compares the
health of persons having different exposures, diets, etc. A case-
control study starts with two defined groups known to differ in
health and compares their exposure characteristics.
---------------------------------------------------------------------------

    Some degree of association between occupational dpm exposure and an
excess prevalence of lung cancer was reported in 41 of the 47 studies
reviewed by MSHA: 22 of the 27 cohort studies and 19 of the 20 case-
control studies. Despite some commenters' use of conflicting
terminology, which will be addressed below, MSHA refers to these 41
studies as ``positive.'' The 22 positive cohort studies in Table III-4
are identified as those reporting a relative risk (RR) or standardized
mortality ratio (SMR) exceeding 1.0. The 19 positive case-control
studies in Table III-5 are identified as those reporting an RR or odds
ratio (OR) exceeding 1.0. A study does not need to be statistically
significant (at the 0.05 level) or meet all criteria described, in
order to be considered a ``positive'' study. The six remaining studies
were entirely negative: they reported a deficit in the prevalence of
lung cancer among exposed workers, relative to whatever population was
used in the study as a basis for comparison. These six negative studies
are identified as those reporting no relative risk (RR), standard
mortality ratio (SMR), or odds ratio (OR) greater than 1.0.\31\
---------------------------------------------------------------------------

    \31\ The six entirely negative studies are: Kaplan (1959);
DeCoufle et al. (1977); Waller (1981); Edling et al. (1987); Bender
et al. (1989); Christie et al. (1995).
---------------------------------------------------------------------------

    MSHA recognizes that these 47 studies are not of equal importance
for determining whether dpm exposure leads to an increased risk of lung
cancer. Some of the studies provide much better evidence than others.
Furthermore, since no epidemiologic study can be perfectly controlled,
the studies exhibit various strengths and weaknesses, as described by
both this risk assessment and a number of commenters. Several
commenters, and some of the reviewers cited above, focused on the
weaknesses and argued that none of the existing studies is conclusive.
MSHA, in accordance with other reviewers and commenters, maintains: (1)
That the weaknesses identified in both negative and positive studies
mainly cause underestimation of risks associated with high occupational
dpm exposure; (2) that it is legitimate to base conclusions on the
combined weight of all available evidence and that, therefore, it is
not necessary for any individual study to be conclusive; and (3) that
even though the 41 positive studies vary a great deal in strength,
nearly all of them contribute something to the weight of positive
evidence.

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[[Page 5592]]

(i) Evaluation Criteria
    Several commenters contended that MSHA paid more attention to
positive studies than to negative ones and indicated that MSHA had not
sufficiently explained its reasons for discounting studies they
regarded as providing negative evidence. MSHA used five principal
criteria to evaluate the strengths and weaknesses of the individual
studies:
    (1) power of the study to detect an exposure effect;
    (2) composition of comparison groups;
    (3) exposure assessment;
    (4) statistical significance; and
    (5) potential confounders.
    These criteria are consistent with those proposed by the HEI Diesel
Epidemiology Expert Panel (HEI, 1999). To help explain MSHA's reasons
for valuing some studies over others, these five criteria will now be
discussed in turn.

Power of the Study

    There are several factors that contribute to a study's power, or
ability to detect an increased risk of lung cancer in an exposed
population. First is the study's size--i.e., the number of subjects in
a cohort or the number of lung cancer cases in a case-control study. If
few subjects or cases are included, then any statistical relationships
are likely to go undetected. Second is the duration and intensity of
exposure among members of the exposed group. The greater the exposure,
the more likely it is that the study will detect an effect if it
exists. Conversely, a study in which few members of the exposed group
experienced cumulative exposures significantly greater than the
background level is unlikely to detect an exposure effect. Third is the
length of time the study allows for lung cancer to exhibit a
statistical impact after exposure begins. This involves a latency
period, which is the time required for lung cancer to develop in
affected individuals, or (mainly pertaining to cohort studies) a
follow-up period, which is the time allotted, including latency, for
lung cancers in affected individuals to show up in the study. It is
generally acknowledged that lung cancer studies should, at the very
minimum, allow for a latency period of at least 10 years from the time
exposure begins and that it is preferable to allow for latency periods
of at least 20 years. The shorter the latency allowance, the less power
the study has to detect any increased risk of lung cancer that may be
associated with exposure.
    As stated above, six of the 47 studies did not show positive
results: One of these studies (Edling et al.) was based on a small
cohort of 694 bus workers, thus having little statistical power. Three
other of these studies (DeCoufle, Kaplan, and Christie) included
exposed workers for whom there was an inadequate latency allowance
(i.e., less than 10 years). The entire period of follow-up in the
Kaplan study was 1953-1958. The Christie study was designed in such a
way as to provide for neither a minimum period of exposure nor a
minimum period of latency: the report covers lung cancers diagnosed
only through 1992, but the ``exposed'' cohort includes workers who may
have entered the work force (and thus begun their exposure) as late as
Dec. 31, 1992. Such workers would not be expected to develop lung
cancer during the study period. The remaining two negative studies
(Bender, 1989 and Waller, 1981) appear to have included a reasonably
adequate number of exposed workers and to have allowed for an adequate
latency period.
    Some of the 41 positive studies also had little power, either
because they included relatively few exposed workers (e.g., Lerchen et
al., 1987, Ahlman et al., 1991; Gustavsson et al., 1990) or an
inadequate latency allowance or follow-up period (e.g., Leupker and
Smith (1978); Milne, 1983; Rushton et al., 1983). In those based on few
exposed workers, there is a strong possibility that the positive
association arose merely by chance.\32\ The other studies, however,
found increased prevalence of lung cancer despite the relatively short
periods of latency and follow-up time involved. It should be noted
that, for reasons other than lack of power, MSHA places very little
weight on the Milne and Rushton studies. As mentioned in Table III-4,
the Rushton study compared the cohort to the national population, with
no adjustment for regional or socioeconomic differences. This may
account for the excess rate of lung cancers reported for the exposed
``general hand'' job category. The Milne study did not control for
potentially important ``confounding'' variables, as explained below in
MSHA's discussion of that criterion.
---------------------------------------------------------------------------

    \32\ As noted in Table III-4, the underground sulfide ore miners
studied by Ahlman et al. (1991) were exposed to radon in addition to
diesel emissions. The total number of lung cancers observed,
however, was greater than what was attributable to the radon
exposure, based on a calculation by the authors. Therefore, the
authors attributed a portion of the excess risk to diesel exposure.
---------------------------------------------------------------------------

Composition of Comparison Groups

    This criterion addresses the question of how equitable is the
comparison between the exposed and unexposed populations in a cohort
study, or between the subjects with lung cancer (i.e., the ``cases'')
and the subjects without lung cancer (i.e., the ``controls'') in a
case-control study. MSHA includes bias due to confounding variables
under this criterion if the groups differ systematically with respect
to such factors as age or exposure to non-diesel carcinogens. For
example, unless adequate adjustments are made, comparisons of
underground miners to the general population may be systematically
biased by the miners' greater exposure to radon gas. Confounding not
built into a study's design or otherwise documented is considered
potential rather than systematic and is considered under a separate
criterion below. Other factors included under the present criterion are
systematic (i.e., ``differential'') misclassification of those placed
into the ``exposed'' and ``unexposed'' groups, selection bias, and bias
due to the ``healthy worker effect.''
    In several of the studies, a group identified with diesel exposure
may have systematically included workers who, in fact, received little
or no occupational diesel exposure. For example, a substantial
percentage of the ``underground miner'' subgroup in Waxweiler et al.
(1973) worked in underground mines with no diesel equipment. This would
have diluted any effect of dpm exposure on the group of underground
miners as a whole.\33\ Similarly, the groups classified as miners in
Benhamou et al. (1988), Boffetta et al. (1988), and Swanson et al.
(1993) included substantial percentages of miners who were probably not
occupationally exposed to diesel emissions. Potential effects of
exposure misclassification are discussed further under the criterion of
``Exposure Assessment'' below.
---------------------------------------------------------------------------

    \33\ Furthermore, as pointed out in comments submitted by Dr.
Peter Valberg through the NMA, the subgroup of underground miners
working at mines with diesel engines was small, and the exposure
duration in one of the mines with diesel engines was only ten years.
Therefore, the power of the study was inadequate to detect an excess
risk of lung cancer for that subgroup by itself.
---------------------------------------------------------------------------

    Selection bias refers to systematic differences in characteristics
of the comparison groups due to the criteria and/or methods used to
select those included in the study. For example, three of the cohort
studies (Raffle, 1957; Leupker and Smith, 1976; Waller, 1981)
systematically excluded retirees from the cohort of exposed workers--
but not

[[Page 5593]]

from the population used for comparison. Therefore, cases of lung
cancer that developed after retirement were counted against the
comparison population but not against the cohort. This artificially
reduced the SMR calculated for the exposed cohort in these three
studies.
    Another type of selection bias may occur when members of the
control group in a case-control study are non-randomly selected. This
happens when cases and controls are selected from the same larger
population of patients or death certificates, and the controls are
simply selected (prior to case matching) from the group remaining after
those with lung cancer are removed. Such selection can lead to a
control group that is biased with respect to occupation and smoking
habits. Specifically, `` * * * a severely distorted estimate of the
association between exposure to diesel exhaust and lung cancer, and a
severely distorted picture of the direction and degree of confounding
by cigarette smoking, can come from case-control studies in which the
controls are a collection of `other deaths' '' when the cause of most
``other deaths'' is itself correlated with smoking or occupational
choice (HEI, 1999). This selection bias can distort results in either
direction.
    MSHA judged that seven of the 20 available case-control studies
were susceptible to this type of selection bias because controls were
drawn from a population of ``other deaths'' or ``other patients.'' \34\
These control groups were likely to have over-represented cases of
cardiovascular disease, which is known to be highly correlated with
smoking and is possibly also correlated with occupation. The only case-
control study not reporting a positive result (DeCoufle et al., 1977)
fell into this group of seven. The remaining 13 case-control studies
all reported positive results.
---------------------------------------------------------------------------

    \34\ These were: Buiatti et al. (1985), Coggan et al. (1984),
DeCoufle et al. (1977), Garshick et al. (1987), Hayes et al. (1989),
Lerchen et al. (1987), and Steenland et al. (1990).
---------------------------------------------------------------------------

    It is ``well established that persons in the work force tend to be
`healthier' than persons not employed, and therefore healthier than the
general population. Worker mortality tends to be below average for all
major causes of death.'' (HEI, 1999) Because workers tend to be
healthier than non-workers, the prevalence of disease found among
workers exposed to a toxic substance may be lower than the rate
prevailing in the general population, but higher than the rate
occurring in an unexposed population of similar workers. This
phenomenon is called the ``healthy worker effect.''
    All five cohort studies reporting entirely negative results drew
comparisons against the general population and made no adjustments to
take the healthy worker effect into account. (Kaplan, 1959; Waller
(1981); Edling et al. (1987); Bender et al. (1989); Christie et al.
(1995)). The sixth negative study (DeCoufle, 1977) was a case-control
study in which vehicle drivers and locomotive engineers were compared
to clerical workers. As mentioned earlier, this study did not meet the
criterion for a minimum 10-year latency period. All other studies in
which exposed workers were compared against similar but unexposed
workers reported some degree of elevated lung cancer risk for exposed
workers.
    Many of the 41 positive studies also drew comparisons against the
general population with no compensating adjustment for the healthy
worker effect. But the healthy worker effect can influence results even
when the age-adjusted mortality or morbidity rate observed among
exposed workers is greater than that found in the general population.
In such studies, comparison with the general population tends to reduce
the excess risk attributable to the substance being investigated. For
example, Gustafsson et al. (1986), Rushton et al. (1983), and Wong et
al. (1985) each reported an unadjusted SMR exceeding 1.0 for lung
cancer in exposed workers and an SMR significantly less than 1.0 for
all causes of death combined. Since the SMR for all causes is less than
1.0, there is evidence of a healthy worker effect. Therefore, the SMR
reported for lung cancer was probably lower than if the comparison had
been made against a more similar population of unexposed workers.
Bhatia et al. (1998) constructed a simple estimate of the healthy
worker effect evident in these studies, based on the SMR for all causes
of death except lung cancer. This estimate was then used to adjust the
SMR reported for lung cancer. For the three positive studies mentioned,
the adjustment raised the SMR from 1.29 to 1.48, from 1.01 to 1.23, and
from 1.07 to 1.34, respectively. \35\
---------------------------------------------------------------------------

    \35\ A similar adjustment was applied to the SMR for lung cancer
reported in one of the negative studies (Edling et al., 1987). This
raised the SMR from 0.67 to 0.80. Because of insufficient data,
Bhatia et al. did not carry out the adjustment for the three other
studies they considered with potentially important healthy worker
effects. (Bhatia et al., 1998)
---------------------------------------------------------------------------

Exposure Assessment

    Many commenters suggested that a lack of concurrent exposure
measurements in available studies limits their utility for quantitative
risk assessment (QRA). MSHA is fully aware of these limitations but
also recognizes that less desirable surrogates of exposure must
frequently be employed out of practical necessity. As stated by HEI's
expert panel on diesel epidemiology:

    Quantitative measures of exposures are important in any
epidemiologic study used for QRA. The greater the detail regarding
specific exposure, including how much, for how long, and at what
concentration, the more useful the study is for this purpose.
Frequently, however, individual measurements are not available, and
surrogate measures or markers are used. For example, the most
general surrogate measures of exposure in occupational epidemiologic
studies are job classification and work location. (HEI, 1999)

    It is important to distinguish, moreover, between studies used to
identify a hazard (i.e., to establish that dpm exposure is associated
with an excess risk of lung cancer) and studies used for QRA (i.e., to
quantify the amount of excess risk corresponding to a given level of
exposure). Although detailed exposure measurements are desirable in any
epidemiologic study, they are more important for QRA than for
identifying and characterizing a hazard. Conversely, epidemiologic
studies can be highly useful for purposes of hazard identification and
characterization even if a lack of personal exposure measurements
renders them less than ideal for QRA.
    Still, MSHA agrees that the quality of exposure assessment affects
the value of a study for even hazard identification. Accordingly, MSHA
has divided the 47 studies into four categories, depending on the
degree to which exposures were quantified for the specific workers
included. This ranking refers only to exposure assessment and does not
necessarily correspond to the overall weight MSHA places on any of the
studies.
    The highest rank, with respect to this criterion, is reserved for
studies having quantitative, concurrent exposure measurements for
specific workers or for specific jobs coupled with detailed work
histories. Only two studies (Johnston et al., 1997 and Saverin et al.,
1999) fall into this category.\36\ Both of these recent cohort studies
took smoking habits into account. These

[[Page 5594]]

studies both reported an excess risk of lung cancer associated with dpm
exposure.
---------------------------------------------------------------------------

    \36\ The study of German potash miners by Saverin et al. was
introduced by NIOSH at the Knoxville public hearing prior to
publication. The study, as cited, was later published in English.
Although the dpm measurements (total carbon) were all made in one
year, the authors provide a justification for assuming that the
mining technology and type of machinery used did not change
substantially during the period miners were exposed (ibid., p.420).
---------------------------------------------------------------------------

    The second rank is defined by semi-quantitative exposure
assessments, based on job history and an estimated exposure level for
each job. The exposure estimates in these studies are crude, compared
to those in the first rank, and they are subject to many more kinds of
error. This severely restricts the utility of these studies for QRA
(i.e., for quantifying the change in risk associated with various
specified exposure levels). For purposes of hazard identification and
characterization, however, crude exposure estimates are better than no
exposure estimates at all. MSHA places two cohort studies and five
case-control studies into this category.\37\ All seven of these studies
reported an excess risk of lung cancer risk associated with diesel
exposure. Thus, results were positive in all nine studies with
quantitative or semi-quantitative exposure assessments.
---------------------------------------------------------------------------

    \37\ The cohort studies are Garshick et al. (1988) and
Gustavsson et al. (1990). The case-control studies are Emmelin et
al. (1993), Garshick et al.(1997), Gustavsson et al. (1990),
Siemiatycki et al. (1988), and Steenland et al. (1990, 1992).
---------------------------------------------------------------------------

    The next rank belongs to those studies with only enough information
on individual workers to construct estimates of exposure duration.
Although these studies present no data relating excess risk to specific
exposure levels, they do provide excess risk estimates for those
working a specified minimum number of years in a job associated with
diesel exposure. One cohort study and five case-control studies fall
into this category, and all six of them reported an excess risk of lung
cancer.\38\ With one exception (Benhamou et al. 1988), these studies
also presented evidence of increased age-adjusted risk for workers with
longer exposures and/or latency periods.
---------------------------------------------------------------------------

    \38\ The cohort study is Wong et al. (1985). The case-control
studies are Bruske-Hohlfeld et al. (1999), Benhamou et al. (1988),
Boffetta et al. (1990), Hayes et al. (1989), and Swanson et al.
(1993).
---------------------------------------------------------------------------

    The bottom rank, with respect to exposure assessment, consists of
studies in which no exposure information was collected for individual
workers. These studies used only job title to distinguish between
exposed and unexposed workers. The remaining 32 studies, including five
of the six with entirely negative results, fall into this category.
    Studies basing exposure assessments on only a current job title (or
even a history of job titles) are susceptible to significant
misclassification of exposed and unexposed workers. Unless the study is
poorly designed, this misclassification is ``nondifferential'' i.e.,
those who are misclassified are no more and no less likely to develop
lung cancer (or to have been exposed to carcinogens such as tobacco
smoke) than those who are correctly classified. If workers are
sometimes misclassified nondifferentially, then this will tend to mask
or dilute any excess risk attributable to exposure. Furthermore,
differential misclassification in these studies usually consists of
systematically including workers with little or no diesel exposure in a
job category identified as ``exposed.'' This too would generally mask
or dilute any excess risk attributable to exposure. Therefore, MSHA
assumes that in most of these studies, more rigorous and detailed
exposure assessments would have resulted in somewhat higher estimates
of excess risk.
    IMC Global, MARG, and some other commenters expressed special
concern about potential exposure misclassification and suggested that
such misclassification might be partly responsible for results showing
excess risk. IMC Global, for example, quoted a textbook observation
that, contrary to popular misconceptions, nondifferential exposure
misclassification can sometimes bias results away from the null. MSHA
recognizes that this can happen under certain special conditions.
However, there is an important distinction between ``can sometimes''
and ``can frequently.'' There is an even more important distinction
between ``can sometimes'' and ``in this case does.'' As noted by the
HEI Expert Panel on Diesel Epidemiology (HEI, 1999, p.48), ``* * *
nondifferential misclassification most often leads to an overall
underestimation of effect.'' Similarly, Silverman (1998) noted,
specifically with respect to the diesel studies, that ``* * * this
[exposure misclassification] bias is most likely to be nondifferential,
and the effect would probably have been to bias point estimates [of
excess risk] toward the null value.''

Statistical Significance

    A ``statistically significant'' finding is a finding unlikely to
have arisen by chance in the particular group, or statistical sample,
of persons being studied. An association arising by chance would have
no predictive value for exposed workers outside the sample. However, a
specific epidemiologic study may fail to achieve statistical
significance for two very different reasons: (1) there may be no real
difference in risk between the two groups being compared, or (2) the
study may lack the power needed to detect whatever difference actually
exists. As described earlier, a lack of sufficient power comes largely
from limitations such as a small number of subjects in the sample, low
exposure and/or duration of exposure, or too short a period of latency
or follow-up time. Therefore, a lack of statistical significance in an
individual study does not demonstrate that the results of that study
were due merely to chance--only that the study (viewed in isolation) is
statistically inconclusive.
    As explained earlier, MSHA classifies a reported RR, SMR, or OR
(i.e., the point estimate of relative risk) as ``positive'' if it
exceeds 1.0 and ``negative'' if it is less than or equal to 1.0. By
common convention, a positive result is considered statistically
significant if its 95-percent confidence interval does not overlap 1.0.
If all other relevant factors are equal, then a statistically
significant positive result provides stronger evidence of an underlying
relationship than one that is not statistically significant. On the
other hand, a study must meet two requirements in order to provide
statistically significant evidence of no positive relationship: (1) the
upper limit of its 95-percent confidence interval must not exceed 1.0
by an appreciable amount \39\ and (2) it must have allowed for
sufficient exposure, latency, and follow-up time to have detected an
existing relationship.
---------------------------------------------------------------------------

    \39\ As a matter of practicality, MSHA places the threshold at
1.05.
---------------------------------------------------------------------------

    As shown in Tables III-4 and III-5, statistically significant
positive results were reported in 25 of the 47 studies: 11 of the 19
positive case-control studies and 14 of the 22 positive cohort studies.
In 16 of the 41 studies showing a positive association, the association
observed was not statistically significant. Results in five of the six
negative studies were not statistically significant. One of the six
negative studies (Christie et al., 1995, in full version), reported a
statistically significant deficit in lung cancer for miners. This
study, however, provided for no minimum period of exposure or latency
and, therefore, lacked the power necessary to provide statistically
significant evidence.\40\
---------------------------------------------------------------------------

    \40\ More detailed discussion of this study appears later in
this subsection.
---------------------------------------------------------------------------

    Whether or not a study provides statistically significant evidence
is dependent upon many variables, such as study size, adequate follow-
up time (to account for enough exposure and latency), and adequate case
ascertainment. In the ideal world, a

[[Page 5595]]

sufficiently powerful study that failed to demonstrate a statistically
significant positive relationship would, by its very failure, provide
statistically significant evidence that an underlying relationship
between an exposure and a specific disease was unlikely. It is
important to note that MSHA regards a real 10-percent increase in the
risk of lung cancer (i.e., a relative risk of 1.1) as constituting a
clearly significant health hazard. Therefore, ``sufficiently powerful''
in this context means that the study would have to be of such scale and
quality as to detect a 10-percent increase in risk if it existed. The
outcome of such a study could plausibly be called ``negative'' even if
the estimated RR slightly exceeded 1.0--so long as the lower confidence
limit did not exceed 1.0 and the upper confidence limit did not exceed
1.05. Rarely does an epidemiological study fall into this ``ideal''
study category. MSHA reviewed the dpm epidemiologic studies to
determine which of them could plausibly be considered to be negative.
    For example, one study (Waxweiller et al., 1973) reported positive
but statistically non-significant results corresponding to an RR of
about 1.1. Among the studies MSHA counts as positive, this is the one
that is numerically closest to being ``negative''. This study, however,
relied on a relatively small cohort containing an indeterminate but
probably substantial percentage of occupationally unexposed workers.
Furthermore, there was no minimum latency allowance for the exposed
workers. Therefore, even if MSHA were to use 1.1 rather than 1.05 as a
threshold for significant relative risk, the study had insufficient
statistical power to merit ``negative'' status.
    One commenter (Dr. James Weeks, representing the UMWA) argued that
``MSHA's reliance on * * * statistical significance is somewhat
misplaced. Results that are not significant statistically * * * can
nevertheless indicate that the exposure in question caused the
outcome.'' MSHA agrees that an otherwise sound study may yield positive
(or negative) results that provide valuable evidence for (or against)
an underlying relationship but fail, because of an insufficient number
of exposed study subjects, to achieve statistical significance. In the
absence of other evidence to the contrary, a single positive but not
statistically significant result could even show that a causal
relationship is more likely than not. By definition, however, such a
result would not be conclusive at a high level of confidence. A finding
of even very high excess risk in a single, well-designed study would be
far from conclusive if based on a very small number of observed lung
cancer cases or if it were in conflict with evidence from toxicity
studies.
    MSHA agrees that evidence should not be ignored simply because it
is not conclusive at a conventional but arbitrary 95-percent confidence
level. Lower confidence levels may represent weaker but still important
evidence. Nevertheless, to rule out chance effects, the statistical
significance of individual studies merits serious consideration when
only a few studies are available. That is not the case, however, for
the epidemiology literature relating lung cancer to diesel exposure.
Since many studies contribute to the overall weight of evidence, the
statistical significance of individual studies is far less important
than the statistical significance of all findings combined. Statistical
significance of the combined findings is addressed in Subsection
3.a.iii of this risk assessment.

Potential Confounders

    There are many variables, both known and unknown, that can
potentially distort the results of an epidemiologic study. In studies
involving lung cancer, the most important example is tobacco smoking.
Smoking is highly correlated with the development of lung cancer. If
the exposed workers in a study tend to smoke more (or less) than the
population to which they are being compared, then smoking becomes what
is called a ``confounding variable'' or ``confounder'' for the study.
In general, any variable affecting the risk of lung cancer potentially
confounds observed relationships between lung cancer and diesel
exposure. Conspicuous examples are age, smoking habits, and exposure to
airborne carcinogens such as asbestos or radon progeny. Diet and other
lifestyle factors may also be potential confounders, but these are
probably less important for lung cancer than for other forms of cancer,
such as bladder cancer.
    There are two ways to avoid distortion of study results by a
potential confounder: (1) Design the study so that the populations
being compared are essentially equivalent with respect to the
potentially confounding variable; or (2) allow the confounding to take
place, but adjust the results to compensate for its effects. Obviously,
the second approach can be applied only to known confounders. Since no
adjustment can be made for unknown confounders, it is important to
minimize their effects by designing the comparison groups to be as
similar as possible.
    The first approach requires a high degree of control over the two
groups being compared (exposed and unexposed in a cohort study; with
and without lung cancer in a case-control study). For example, the
effects of age in a case-control study can be controlled by matching
each case of lung cancer with one or more controls having the same year
of birth and age in year of diagnosis or death. Matching on age is
never perfect, because it is generally not feasible to match within a
day or even a month. Similarly, the effects of smoking in a case-
control study can be imperfectly controlled by matching on smoking
habits to the maximum extent possible.\41\ In a cohort study, there is
no confounding unless the exposed cohort and the comparison group
differ with respect to a potential confounder. For example, if both
groups consist entirely of never-smokers, then smoking is not a
confounder in the study. If both groups contain the same percentage of
smokers, then smoking is still an important confounder to the extent
that smoking intensity and history differ between the two groups. In an
attempt to minimize such differences (along with potentially important
differences in diet and lifestyle) some studies restrict comparisons to
workers of similar socioeconomic status and area of residence. Studies
may also explicitly investigate smoking habits and histories and forego
any adjustment of results if these factors are found to be
homogeneously distributed across comparison groups. In that case,
smoking would not actually appear to function as a confounder, and a
smoking adjustment might not be required or even desirable.
Nevertheless, a certain amount of smoking data is still necessary in
order to check or verify homogeneity. The study's credibility may also
be an important consideration. Therefore, MSHA agrees with the HEI's
expert panel that even when smoking appears not to be a confounder,

    * * * a study is open to criticism if no smoking data are
collected and the association between exposure and outcome is weak.
* * * When the magnitude of the association of interest is weak,
uncontrolled confounding, particularly from a strong confounder such
as cigarette smoking, can have a major impact on the study's results
and on the credibility of their use. [HEI, 1999]

However, this does not mean that a study cannot, by means of an
efficient study design and/or statistical verification of homogeneity,

[[Page 5596]]

demonstrate adequate control for smoking without applying a smoking
adjustment.
---------------------------------------------------------------------------

    \41\ If cases and controls cannot be closely matched on smoking
or other potentially important confounder, then a hybrid approach is
often taken. Cases and controls are matched as closely as possible,
differences are quantified, and the study results are adjusted to
account for the differences.
---------------------------------------------------------------------------

    The second approach to dealing with a confounder requires knowledge
or estimation both of the differences in group composition with respect
to the confounder and of the effect that the confounder has on lung
cancer. Ideally, this would entail specific, quantitative knowledge of
how the variable affects lung cancer risk for each member of both
groups being compared. For example, a standardized mortality ratio
(SMR) can be used to adjust for age differences when a cohort of
exposed workers with known birth dates is compared to an unexposed
reference population with known, age-dependent lung cancer rates.\42\
In practice, it is not usually possible to obtain detailed information,
and the effects of smoking and other known confounders cannot be
precisely quantified.
---------------------------------------------------------------------------

    \42\ Since these rates may vary by race, geographic region, or
other factors, the validity of this adjustment depends heavily on
choice of an appropriate reference population. For example,
Waxweiler et al. (1973) based SMRs for a New Mexico cohort on
national lung cancer mortality rates. Since the national age-
adjusted rate of lung cancer is about \1/3\ higher than the New
Mexico rate, the reported SMRs were roughly \3/4\ of what they would
have been if based on rates specific to New Mexico.
---------------------------------------------------------------------------

    Stoaber and Abel (1996) argue, along with Morgan et al. (1997) and
some commenters, that even in those epidemiologic studies that are
adjusted for smoking and show a statistically significant association,
the magnitude of relative or excess risk observed is too small to
demonstrate any causal link between dpm exposure and cancer. Their
reasoning is that in these studies, errors in the collection or
interpretation of smoking data can create a bias in the results larger
than any potential contribution attributable to diesel particulate.
They propose that studies failing to account for smoking habits should
be disqualified from consideration, and that evidence of an association
from the remaining, smoking-adjusted studies should be discounted
because of potential confounding due to erroneous, incomplete, or
otherwise inadequate characterization of smoking histories.
    It should be noted, first of all, that five of the six negative
studies neither matched nor adjusted for smoking.\43\ But more
importantly, MSHA concurs with IARC (1989), Cohen and Higgins (1995),
IPCS (1996), CAL-EPA (1998), ACGIH (1998), Bhatia et al. (1998), and
Lipsett and Campleman (1999) in not accepting the view that studies
should automatically be disqualified from consideration because of
potential confounders. MSHA recognizes that unknown exposures to
tobacco smoke or other human carcinogens can distort the results of
some lung cancer studies. MSHA also recognizes, however, that it is not
possible to design a human epidemiologic study that perfectly controls
for all potential confounders. It is also important to note that a
confounding variable does not necessarily inflate an observed
association. For example, if the exposed members of a cohort smoke less
than the reference group to which they are compared, then this will
tend to reduce the apparent effects of exposure on lung cancer
development. In the absence of evidence to the contrary, it is
reasonable to assume that a confounder is equally likely to inflate or
to deflate the results.
---------------------------------------------------------------------------

    \43\ The exception is DeCoufle et al. (1977), a case-control
study that apparently did not match or otherwise adjust for age.
---------------------------------------------------------------------------

    As shown in Tables III-4 and III-5, 18 of the published
epidemiologic studies involving lung cancer did, in fact, control or
adjust for exposure to tobacco smoke, and five of these 18 also
controlled or adjusted for exposure to asbestos and other carcinogenic
substances (Garshick et al., 1987; Boffetta et al., 1988; Steenland et
al., 1990; Morabia et al., 1992; Bruske-Hohlfeld et al., 1999). These
results are less likely to be confounded than results from most of the
studies with no adjustment. All but one of these 18 studies reported
some degree of excess risk associated with occupational exposure to
diesel particulate, with statistically significant results reported in
eight.
    In addition, several of the studies with no smoking adjustment took
the first approach described above for preventing or substantially
mitigating potential confounding by smoking habits: they drew
comparisons against internal control groups or other control groups
likely to have similar smoking habits as the exposed groups (e.g.,
Garshick et al., 1988; Gustavsson et al., 1990; Hansen, 1993; and
Saverin et al., 1999). Therefore, MSHA places more weight on these
studies than on studies drawing comparisons against dissimilar groups
with no smoking controls or adjustments. This emphasis is in accordance
with the conclusion by Bhatia et al. (1998) that smoking homogeneity
typically exists within cohorts and is associated with a uniform
lifestyle and social class. Although it was not yet available at the
time Bhatia et al. performed their analysis, an analysis of smoking
patterns by Saverin et al. (op cit.) within the cohort they studied
also supports this conclusion.
    IMC Global and MARG objected to MSHA's position on potential
confounders and submitted comments in general agreement with the views
of Morgan et al. (op cit.) and Stobel and Abel (op cit.). Specifically,
they suggested that studies reporting relative risks solely between 1.0
and 2.0 should be discounted because of potential confounders. Of the
41 positive studies considered by MSHA, 22 fall into this category (16
cohort and 6 case-control). In support of their suggestion, IMC Global
quoted Speizer (1986), Muscat and Wynder (1995), Lee (1989), WHO
(1980), and NCI (1994). These authorities all urged great caution when
interpreting the results of such studies, because of potential
confounders. MSHA agrees that none of these studies, considered
individually, is conclusive and that each result must be considered
with due caution. None of the quoted authorities, however, proposed
that such studies should automatically be counted as ``negative'' or
that they could not add incrementally to an aggregate body of positive
evidence.
    IMC Global also submitted the following reference to two Federal
Court decisions pertaining to estimated relative risks less than 2.0:

    The Ninth Circuit concluded in Daubert v. Merrell Dow
Pharmaceuticals'' that ``for an epidemiologic study to show
causation * * * the relative risk * * * arising from the
epidemiologic data will, at a minimum, have to exceed 2.''
Similarly, a District Court stated in Hall v. Baxter Healthcare
Corp.49: The threshold for concluding that an agent was more likely
the cause of the disease than not is relative risk greater than 2.0.
Recall that a relative risk of 1.0 means that the agent has no
affect on the incidence of disease. When the relative risk reaches
2.0. the agent is responsible for an equal number of cases of
disease as all other background causes. Thus a relative risk of 2.0
implies a 50% likelihood that an exposed individual's disease was
caused by the agent. [IMC Global]

    In contrast with the two cases cited, the purpose of this risk
assessment is not to establish civil liabilities for personal injury.
MSHA's concern is with reducing the risk of lung cancer, not with
establishing the specific cause of lung cancer for an individual miner.
The excess risk of an outcome, given an excessive exposure, is not the
same thing as the likelihood that an excessive exposure caused the
outcome in a given case. To understand the difference, it may be
helpful to consider two analogies: (1) The likelihood that a given
death was caused by a lightning strike is relatively low, yet exposure
to lightning is rather hazardous; (2) a specific smoker may not be able
to prove that his or her lung cancer was

[[Page 5597]]

``more likely than not'' caused by radon exposure, yet radon exposure
significantly increases the risk--especially for smokers. Lung cancer
has a variety of alternative causes, but this fact does not reduce the
risk associated with any one of them.
    Furthermore, there is ample precedent for utilizing epidemiologic
studies reporting relative risks less than 2.0 in making clinical and
public policy decisions. For example, the following table contains the
RR for death from cardiovascular disease associated with cigarette
smoking reported in several prospective epidemiologic studies:

------------------------------------------------------------------------
                                                          Estimate of RR
                                                           of death from
               Study on cigarette smoking                 cardiovascular
                                                              disease
------------------------------------------------------------------------
British doctors.........................................           1.6
Males in 25 states:                                       ..............
    Ages 45-64..........................................           2.08
    Ages 65-79..........................................           1.36
U.S. Veterans...........................................           1.74
Japanese study..........................................           1.96
Canadian veterans.......................................           1.6
Males in nine states....................................           1.70
Swedish males...........................................           1.7
Swedish females.........................................           1.3
California occupations..................................           2.0
------------------------------------------------------------------------
Source: U.S. Department of Health and Human Services (1989).

    By IMC Global's rule of thumb, all but one or two of these studies
would be discounted as evidence of increased risk attributable to
smoking. These studies, however, have not been widely discounted by
scientific authorities. To the contrary, they have been instrumental in
establishing that cigarette smoking is a principal cause of heart
disease.
    A second example is provided by the increased risk of lung cancer
found to be caused by residential exposure to radon progeny. As in the
case of dpm, tobacco smoking has been an important potential confounder
in epidemiological studies used to investigate whether exposures to
radon concentrations at residential levels can cause lung cancer. Yet,
in the eight largest residential epidemiological studies used to help
establish the reality of this now widely accepted risk, the reported
relative risks were all less than 2.0. Based on a meta-analysis of
these eight studies, the combined relative risk of lung cancer
attributable to residential radon exposure was 1.14. This elevation in
the risk of lung cancer, though smaller than that reported in most
studies of dpm effects, was found to be statistically significant at a
95-percent confidence level (National Research Council, 1999, Table G-
25).
(ii) Studies Involving Miners
    In the proposed risk assessment, MSHA identified seven
epidemiologic studies reporting an excess risk of lung cancer among
miners thought to have been exposed occupationally to diesel exhaust.
As stated in the proposal, two of these studies specifically
investigated miners, and the other five treated miners as a subgroup
within a larger population of workers.\44\ MSHA placed two additional
studies specific to exposed coal miners (Christie et al., 1995;
Johnston et al.,1997) into the public record with its Feb. 12, 1999
Federal Register notice. Another study,\45\ investigating lung cancer
in exposed potash miners, was introduced by NIOSH at the Knoxville
public hearing on May 27, 1999 and later published as Saverin et al.,
1999. Finally, one study reporting an excess risk of lung cancer for
presumably exposed miners was listed in Table III-5 as originally
published, and considered by MSHA in its overall assessment, but
inadvertently left out of the discussion on studies involving miners in
the previous version of this risk assessment.\46\ There are, therefore,
available to MSHA a total of 11 epidemiologic studies addressing the
risk of lung cancer for miners, and five of these studies are specific
to miners.
---------------------------------------------------------------------------

    \44\ In the proposed risk assessment, the studies identified as
specifically investigating miners were Waxweiler et al. (1973) and
Ahlman et al. (1991). At the Albuquerque public hearing, Mr. Bruce
Watzman, representing the NMA, asked a member of the MSHA panel (Mr.
Jon Kogut) to list six studies involving miners that he had cited
earlier in the hearing and to identify those that were specific to
miners. In both his response to Mr. Watzman, and in his earlier
remarks, Mr. Kogut noted that the studies involving miners were
listed in Tables III-4 and III-5. However, he inadvertently
neglected to mention Ahlman et al. (op cit.) and Morabia et al.
(1992). (The latter study addressed miners as a subgroup of a larger
population.)
    In his response to Mr. Watzman, Mr. Kogut cited Swanson et al.
(1993) but not Burns and Swanson (1991), which he had mentioned
earlier in the hearing in connection with the same study. These two
reports are listed under a single entry in Table III-5 (Swanson et
al.) because they both report findings based on the same body of
data. Therefore, MSHA considers them to be two parts of the same
study. The 5.03 odds ratio for mining machine operators mentioned by
Mr. Kogut during the hearing was reported in Burns and Swanson
(1991).
    Only the six studies specified by Mr. Kogut in his response to
Mr. Watzman were included in separate critiques by Dr. Peter Valberg
and Dr. Jonathan Borak later submitted by the NMA and by MARG,
respectively. Dr. Valberg did not address Burns and Swanson (1991),
and he addressed a different report by Siemiatycki than the one
listed in Table III-5 and cited during the hearing (i.e.,
Siemiatycki et al., 1988). Neither Dr. Valberg nor Dr. Borak
addressed Ahlman et al. (op cit.) or Morabia et al. (op cit.). Also
excluded were two additional miner-specific studies placed into the
record on Feb. 12, 1999 (Fed Reg. 64:29 at 59258). Mr. Kogut did not
include them in his response to Mr. Watzman, or in his prior
remarks, because he was referring only to studies listed in Tables
III-4 and III-5 of the published proposals. Mr. Kogut also did not
include a study specific to German potash miners submitted by NIOSH
at a subsequent public hearing, and this too was left out of both
critiques. A published version of the study (Saverin et al., 1999)
was placed into the record on June 30, 2000. All of the studies
involving miners are in the public record and have been available
for comment by interested parties throughout the posthearing comment
periods.
    \45\ Some commenters suggested that MSHA ``overlooked'' a
recently published study on NSW miners, Brown et al., 1997. This
study evaluated the occurrence of forms of cancer other than lung
cancer in the same cohort studied by Christie et al. (1995).
    \46\ This study was published in two separate reports on the
same body of data: Burns and Swanson (1991) and Swanson et al.
(1993). Both published reports are listed in Table III-5 under the
entry for Swanson et al.
---------------------------------------------------------------------------

    Five cohort studies (Waxweiler et al.,1973; Ahlman et al., 1991;
Christie et al., 1996; Johnston et al., 1997; Saverin et al., 1999)
were performed specifically on groups of miners, and one (Boffetta et
al., 1988) addressed miners as a subgroup of a larger population.
Except for the study by Christie et al., the cohort studies all showed
elevated lung cancer rates for miners in general or for the most highly
exposed miners within a cohort. In addition, all five case-control
studies reported elevated rates of lung cancer for miners (Benhamou et
al.,1988; Lerchen et al., 1987; Siemiatycki et al.,1988; Morabia et
al., 1992; Burns and Swanson, 1991).
    Despite the risk assessment's emphasis on human studies, some
members of the mining community apparently believed that the risk
assessment relied primarily on animal studies and that this was because
studies on miners were unavailable. Canyon Fuels, for example,
expressed concerns about relying on animal studies instead of studies
on western diesel-exposed miners:

    Since there are over a thousand miners here in the West that
have fifteen or more years of exposure to diesel exhaust, why has
there been no study of the health status of those miners? Why must
we rely on animal studies that are questionable and inconclusive?

Actually, western miners were involved in several studies of health
effects other than cancer, as described earlier in this risk
assessment. With respect to lung cancer, there are many reasons why
workers from a particular group of mines might not be selected for
study. Lung cancer often takes considerably more than 15 years to
develop, and a valid study must allow not only for adequate duration of
exposure but also for an adequate period of latency following exposure.
Furthermore, many mines contain radioactive gases and/or

[[Page 5598]]

respirable silica dust, making it difficult to isolate the effects of a
potential carcinogen.
    Similarly, at the public hearing in Albuquerque on May 13, 1999, a
representative of Getchell Gold stated that he thought comparing miners
to rats was irrational and that ``there has not been a study on these
miners as to what the effects are.'' To correct the impression that
MSHA was basing its risk assessment primarily on laboratory animal
studies, an MSHA panelist pointed out Tables III-4 and III-5 of the
proposed preamble and identified six studies pertaining to miners that
were listed in those tables. However, he placed no special weight on
these studies and cited them only to illustrate the existence of
epidemiologic studies reporting an elevated risk of lung cancer among
miners.
    With their post-hearing comments, the NMA and MARG submitted
critiques by Dr. Peter Valberg and Dr. Jonathan Borak of six reports
involving miners (see Footnote 42). Drs. Valberg and Borak both noted
that the six studies reviewed lacked information on diesel exposure and
were vulnerable to confounders and exposure misclassification. For
these reasons, Dr. Valberg judged them ``particularly poor in
identifying what specific role, if any, diesel exhaust plays in lung
cancer for miners.'' He concluded that they do not ``implicate diesel
exposure per se as strongly associated with lung cancer risk in
miners.'' Similarly, Dr. Borak suggested that, since they do not relate
adverse health effects in miners to any particular industrial exposure,
``the strongest conclusion that can be drawn from these six studies is
that the miners in the studies had an increased risk of lung cancer.''
    MSHA agrees with Drs. Valberg and Borak that none of the studies
they reviewed provides direct evidence of a link between dpm exposure
and the excess risk of lung cancer reported for miners. (A few
disagreements on details of the individual studies will be discussed
below). As MSHA said at the Albuquerque hearing, the lack of exposure
information on miners in these studies led MSHA to rely more heavily on
associations reported for other occupations. MSHA also noted the
limitations of these studies in the proposed risk assessment. MSHA
explicitly stated that other epidemiologic studies exist which, though
not pertaining specifically to mining environments, contain better
diesel exposure information and are less susceptible to confounding by
extraneous risk factors.
    Inconclusive as they may be on their own, however, even studies
involving miners with only presumed or sporadic occupational diesel
exposure can contribute something to the weight of evidence. They can
do this by corroborating evidence of increased lung cancer risk for
other occupations with likely diesel exposures and by providing results
that are at least consistent with an increased risk of lung cancer
among miners exposed to dpm. Moreover, two newer studies pertaining
specifically to miners do contain dpm exposure assessments based on
concurrent exposure measurements (Johnston et al., op cit.; Saverin et
al.,op cit.). The major limitations pointed out by Drs. Valberg and
Borak with respect to other studies involving miners do not apply to
these two studies.

Case-Control Studies

    Five case-control studies, all of which adjusted for smoking, found
elevated rates of lung cancer for miners, as shown in Table III-5. The
results for miners in three of these studies (Benhamou et al., 1988;
Morabia et al., 1992; Siemiatycki et al., 1988) are given little
weight, partly because of possible confounding by occupational exposure
to radioactive gasses, asbestos, and silica dust. Also, Benhamou and
Morabia did not verify occupational diesel exposure status for the
miners. Siemiatycki performed a large number of multiple comparisons
and reported that most of the miners ``were exposed to diesel exhaust
for short periods of time,'' Lerchen et al. (1987) showed a marginally
significant result for underground non-uranium miners, but cases and
controls were not matched on date of birth or death, and the frequency
of diesel exposure and exposure to known occupational carcinogens among
these miners was not reported.
    Burns and Swanson (1991) \47\ reported elevated lung cancer risk
for miners and especially mining machine operators, which the authors
attributed to diesel exposure. Potential confounding by other
carcinogens associated with mining make the results inconclusive, but
the statistically significant odds ratio of 5.0 reported for mining
machine operators is high enough to cause concern with respect to
diesel exposures, especially in view of the significantly elevated
risks reported in the same study for other diesel-exposed occupations.
The authors noted that the ``occupation most likely to have high levels
of continuous exposure to diesel exhaust and to experience that
exposure in a confined area has the highest elevated risks: mining
machine operators.''
---------------------------------------------------------------------------

    \47\ This report is listed in Table III-5 under Swanson et al.
(1993), which provides further analysis of the same body of data.
---------------------------------------------------------------------------

Cohort Studies

    As shown in Table III-4, MSHA identified six cohort studies
reporting results for miners likely to have been exposed to dpm. An
elevated risk of lung cancer was reported in five of these six studies.
These results will be discussed chronologically.
    Waxweiller (1973) investigated a cohort of underground and surface
potash miners. The authors noted that potash ore ``is not embedded in
siliceous rock'' and that the ``radon level in the air of potash mines
is not significantly higher than in ambient air.'' Contrary to Dr.
Valberg's review of this study, the number of lung cancer cases was
reported to be slightly higher than expected, for both underground and
surface miners, based on lung cancer rates in the general U.S.
population (after adjustment for age, sex, race, and date of death).
Although the excess was not statistically significant, the authors
noted that lung cancer rates in the general population of New Mexico
were about 25 percent lower than in the general U.S. population. They
also noted that a higher than average percentage of the miners smoked
and that this would ``tend to counterbalance'' the adjustment needed
for geographic location. The authors did not, however, consider two
other factors that would tend to obscure or deflate an excess risk of
lung cancer, if it existed: (1) A healthy worker effect and (2) the
absence of any occupational diesel exposure for a substantial
percentage of the underground miners.
    MSHA agrees with Dr. Valberg's conclusion that ``low statistical
power and indeterminate diesel-exhaust exposure render this study
inadequate for assessing the effect of diesel exhaust on lung-cancer
risk in miners.'' However, given the lack of any adjustment for a
healthy worker effect, and the likelihood that many of the underground
miners were occupationally unexposed, MSHA views the slightly elevated
risk reported in this study as consistent with other studies showing
significantly greater increases in risk for exposed workers.
    Boffetta et al. (1988) investigated mortality in a cohort of male
volunteers who enrolled in a prospective study conducted by the
American Cancer Society. Lung cancer mortality was analyzed in relation
to self-reported diesel exhaust exposure and to employment in various
occupations

[[Page 5599]]

identified with diesel exhaust exposure, including mining. After
adjusting for smoking patterns,\48\ there was a statistically
significant excess of 167 percent (RR = 2.67) in lung cancers among
2034 workers ever employed as miners, compared to workers never
employed in occupations associated with diesel exposure. No analysis by
type of mining was reported. Other findings reported from this study
are discussed in the next subsection.
---------------------------------------------------------------------------

    \48\ During the public hearing on May 25, 1999, Mr. Mark
Kaszniak of IMC Global incorrectly asserted that ``smoking was
treated in a simplistic way in this study by using three categories:
smokers, ex-smokers, and non-smokers.'' The study actually used five
categories, dividing smokers into separate categories for 1-20
cigarettes per day, 21 or more cigarettes per day, and exclusively
pipe and/or cigar smoking.
---------------------------------------------------------------------------

    Although an adjustment was made for smoking patterns, the relative
risk reported for mining did not control for exposures to radioactive
gasses, silica dust, and asbestos. These lung carcinogens are probably
present to a greater extent in mining environments than in most of the
occupational environments used for comparison. Self-reported exposures
to asbestos and stone dusts were taken into account in other parts of
the study, but not in the calculation of excess lung cancer risks
associated with specific occupations, including mining.
    Several commenters reiterated two caveats expressed by the study's
authors and noted in Table III-4. These are (1) that the study is
susceptible to selection biases because participants volunteered and
because the age-adjusted mortality rates differed between those who
provided exposure information and those who did not; and (2) that all
exposure information was self-reported with no quantitative
measurements. Since these caveats are not specific to mining and
pertain to most of the study's findings, they will be addressed when
this study's overall results are described in the next subsection.
    One commenter, however (Mr. Mark Kaszniak of IMC Global), argued
that selection bias due to unknown diesel exposure status played an
especially important role in the RR calculated for miners. About 21
percent of all participants provided no diesel exposure information.
Mr. Kaszniak noted that diesel exposure status was unknown for an even
larger percentage of miners and suggested that the RR calculated for
miners was, therefore, inflated. He presented the following argument:

    In the miner category, this [unknown diesel exposure status]
accounted for 44.2% of the study participants, higher than any other
occupation studied. This is important as this group experienced a
higher mortality for all causes as well as lung cancer than the
analyzed remainder of the cohort. If these persons had been included
in the ``no exposure to diesel exhaust group,'' their inclusion
would have lowered any risk estimates from diesel exposure because
of their higher lung cancer rates. [IMC Global post-hearing
comments]

    This argument, which was endorsed by MARG, was apparently based on
a misunderstanding of how the comparison groups used to generate the RR
for mining were defined.\49\ Actually, persons with unknown diesel
exposure status were included among the miners, but excluded from the
reference population. Including sometime miners with unknown diesel
exposure status in the ``miners'' category would tend to mask or reduce
any strong association that might exist between highly exposed miners
and an increased risk of lung cancer. Excluding persons with unknown
exposure status from the reference population had an opposing effect,
since they happened to experience a higher rate of lung cancer than
cohort members who said they were unexposed. Therefore, removing
``unknowns'' from the ``miner'' group and adding them to the reference
group could conceivably shift the calculated RR for miners in either
direction. However, the RR reported for persons with unknown diesel
exposure status, compared to unexposed persons, was 1.4 (ibid., p.
412)--which is smaller than the 2.67 reported for miners. Therefore, it
appears more likely that the RR for mining was deflated than inflated
on account of persons with unknown exposure status.
---------------------------------------------------------------------------

    \49\ During the public hearing on May 25, 1999, Mr. Kaszniak
stated his belief that, for miners, the ``relative risk calculation
excluded that 44% of folks who did not respond to the questionnaire
with regards to diesel exposure.'' Contrary to Mr. Kaszniak's
belief, however, the ``miners'' on which the 2.67 RR was based
included all 2034 cohort members who had ever been a miner,
regardless of whether they had provided diesel exposure information
(see Boffetta et al., 1988, p. 409).
    Furthermore, the 44.2-percent nonrespondent figure is not
pertinent to potential selection bias in the RR calculation reported
for miners. The group of 2034 ``sometime'' miners used in that
calculation was 65 percent larger than the group of 1233 ``mainly''
miners to which the 44-percent nonrespondent rate applies. The
reference group used for comparison in the calculation consisted of
all cohort members ``with occupation different from those listed
[i.e., railroad workers, truck drivers, heavy equipment operators,
and miners] and not exposed [to diesel exhaust].'' The overall
nonrespondent rate for occupations in the reference group was about
21 percent (calculated by MSHA from Table VII of Boffetta et al.,
1988).
---------------------------------------------------------------------------

    Although confounders and selection effects may have contributed to
the 2.67 RR reported for mining, MSHA believes this result was high
enough to support a dpm effect, especially since elevated lung cancer
rates were also reported for the three other occupations associated
with diesel exhaust exposure. Dr. Borak stated without justification
that ``[the] association between dpm and lung cancer was confounded by
age, smoking, and other occupational exposures * * *.'' He ignored the
well-documented adjustments for age and smoking. Although it does not
provide strong or direct evidence that dpm exposure was responsible for
any of the increased risk of lung cancer observed among miners, the RR
for miners is consistent with evidence provided by the rest of the
study results.
    Ahlman et al. (1991) studied cohorts of 597 surface miners and 338
surface workers employed at two sulfide ore mines using diesel powered
front-end loaders and haulage equipment. Both of these mines (one
copper and one zinc) were regularly monitored for alpha energy
concentrations (i.e., due to radon progeny), which were at or below the
Finish limit of 0.3 WL throughout the study period. The ore in both
mines contained arsenic only as a trace element (less than 0.005
percent). Lung cancer rates in the two cohorts were compared to rates
for males in the same province of Finland. Age-adjusted excess
mortality was reported for both lung cancer and cardiovascular disease
among the underground miners, but not among the surface workers. None
of the underground miners who developed lung cancer had been
occupationally exposed to asbestos, metal work, paper pulp, or organic
dusts. Based on the alpha energy concentration measurements made for
the two mines, the authors calculated that not all of the excess lung
cancer for the underground miners was attributable to radon exposure.
Based on a questionnaire, the authors found similar underground and
surface age-specific smoking habits and alcohol consumption and
determined that ``smoking alone cannot explain the difference in lung
cancer mortality between the [underground] miners and surface workers.
Due to the small size of the cohort, the excess lung cancer mortality
for the underground miners was not statistically significant. However,
the authors concluded that the portion of excess lung cancer not
attributable to radon exposure could be explained by the combined
effects of diesel exhaust and silica exposure. Three of the ten lung
cancers reported for underground miners were experienced by conductors
of diesel-powered ore trains.
    Christie et al. (1994, 1995) studied mortality in a cohort of
23,630 male Australian (New South Wales, NSW)

[[Page 5600]]

coal mine workers who entered the industry after 1972. Although the
majority of these workers were underground miners, most of whom were
presumably exposed to diesel emissions, the cohort included office
workers and surface (``open cut'') miners. The cohort was followed up
through 1992. After adjusting for age, death rates were lower than
those in the general male population for all major causes except
accidents. This included the mortality rate for all cancers as a group
(Christie et al., 1995, Table 1). Lower-than-normal incidence rates
were also reported for cancers as a group and for lung cancer
specifically (Christie et al., 1994, Table 10).
    The investigators noted that the workers included in the cohort
were all subject to pre-employment physical examinations. They
concluded that ``it is likely that the well known `healthy worker'
effect * * * was operating'' and that, instead of comparing to a
general population, ``a more appropriate comparison group is Australian
petroleum industry workers.'' (Christie et al., 1995) In contrast to
the comparison with the population of NSW, the all-cause standardized
mortality ratio (SMR) for the cohort of coal miners was greater than
for petroleum workers by a factor of over 20 percent--i.e., 0.76 vs.
0.63 (ibid., p. 20). However, the investigators did not compare the
cohort to petroleum workers specifically with respect to lung cancer or
other causes of death. Nor did they adjust for a healthy worker effect
or make any attempt to compare mortality or lung cancer rates among
workers with varying degrees of diesel exposure within the cohort.
    Despite the elevated SMR relative to petroleum workers, several
commenters cited this study as evidence that exposure to diesel
emissions was not causally associated with an increased risk of lung
cancer (or with adverse health effects associated with fine
particulates). These commenters apparently ignored the investigators'
explanation that the low SMRs they reported were likely due to a
healthy worker effect. Furthermore, since the cohort exhibited lower-
than-normal mortality rates due to heart disease and non-cancerous
respiratory disease, as well as to cancer, there may well have been
less tobacco smoking in the cohort than in the general population.
Therefore, it is reasonably likely that the age-adjusted lung cancer
rate would have been elevated, if it had been adjusted for smoking and
for a healthy worker effect based on mortality from causes other than
accidents or respiratory disease. In addition, the cohort SMR for
accidents (other than motor vehicle accidents) was significantly above
that of the general population. Since the coal miners experienced an
elevated rate of accidental death, they had a lower-than-normal chance
to die from other causes or to develop lung cancer. The investigators
made no attempt to adjust for the competing, elevated risk of death due
to occupational accidents.
    Given the lack of any adjustment for smoking, healthy worker
effect, or the competing risk of accidental death, the utility of this
study in evaluating health consequences of Dpm exposure is severely
limited by its lack of any internal comparisons or comparisons to a
comparable group of unexposed workers. Furthermore, even if such
adjustments or comparisons were made, several other attributes of this
study limit its usefulness for evaluating whether exposure to diesel
emissions is associated with an increased risk of lung cancer. First,
the study was designed in such a way as to allow inadequate latency for
a substantial portion of the cohort. Although the cohort was followed
up only through 1992, it includes workers who entered the workforce at
the end of 1992. Therefore, there is no minimum duration of
occupational exposure for members of the cohort. Approximately 30
percent of the cohort was employed in the industry for less than 10
years, and the maximum duration of employment and latency combined was
20 years. Second, average age for members of the cohort was only 40 to
50 years (Christie et al., p. 7), and the rate of lung cancer was based
on only 29 cases. The investigators acknowledged that ``it is a
relatively young cohort'' and that ``this means a small number of
cancers available for analysis, because cancer is more common with
advancing age * * *.'' They further noted that ``* * * the number of
cancers available for analysis is increasing very rapidly. As a
consequence, every year that passes makes the cancer experience of the
cohort more meaningful in statistical terms.'' (ibid., p. 27) Third,
miners's work history was not tracked in detail, beyond identifying the
first mine in which a worker was employed. Some of these workers may
have been employed, for various lengths of time, in both underground
and surface operations at very different levels of diesel exposure.
Without detailed work histories, it is not possible to construct even
semi-quantitative measures of diesel exposure for making internal
comparisons within the cohort.
    One commenter (MARG) claimed that this (NSW) study ``* * * reflects
the latest and best scientific evidence, current technology, and the
current health of miners'' and that it ``is not rational to predicate
regulations for the year 2000 and beyond upon older scientific studies
* * *.'' For the reasons stated above, MSHA believes, to the contrary,
that the NSW study contributes little or no information on the
potential health effects of long-term dpm exposures and that whatever
information it does contribute does not extend to effects, such as
cancer, expected in later life.
    Furthermore, three even more recent studies are available that MSHA
regards as far more informative for the purposes of the present risk
assessment. Unlike the NSW study, these directly address Dpm exposure
and the risk of lung cancer. Two of these studies (Johnston et al.,
1997; Saverin et al., 1999), both incorporating a quantitative Dpm
exposure assessment, were carried out specifically on mining cohorts
and will be discussed next. The third (Bruske-Hohlfeld et al., 1999) is
a case-control study not restricted to miners and will be discussed in
the following subsection. In accordance with MARG's emphasis on the
timeliness of scientific studies, MSHA places considerable weight on
the fact that all three--the most recent epidemiologic studies
available--reported an association between diesel exposure and an
increased risk of lung cancer.
    Johnston et al. (1997) studied a cohort of 18,166 coal miners
employed in ten British coal mines over a 30-year period. Six of these
coal mines used diesel locomotives, and the other four were used for
comparison. Historical NOX and respirable dust concentration
measurements were available, having routinely been collected for
monitoring purposes. Two separate approaches were taken to estimate dpm
exposures, leading to two different sets of estimates. The first
approach was based on NOX measurements, combined with
estimated ratios between dpm and NOX. The second approach
was based on complex calculations involving measurements of total
respirable dust, ash content, and the ratio of quartz to dust for
diesel locomotive drivers compared to the ratio for face workers
(ibid., Figure 4.1 and pp 25-46). These calculations were used to
estimate dpm exposure concentrations for the drivers, and the estimates
were then combined with traveling times and dispersion rates to form
estimates of dpm concentration levels for other occupational groups. In
four of the six dieselized mines, the NOX-based and dust-
based estimates of dpm were in generally good agreement, and they

[[Page 5601]]

were combined to form time-independent estimates of shift average dpm
concentration for individual seams and occupational groups within each
mine. In the fifth mine, the PFR measurements were judged unreliable
for reasons extensively discussed in the report, so the NOX-
based estimates were used. There was no NOX exposure data
for the sixth mine, so they used dust-based estimates of dpm exposure.
    Final estimates of shift-average dpm concentrations ranged from 44
g/m\3\ to 370 g/m\3\ for locomotive drivers and from
1.6 g/m\3\ to 40 g/m\3\ for non-drivers at various
mines and work locations (ibid.,Tables 8.3 and 8.6, respectively).
These were combined with detailed work histories, obtained from
employment records, to provide an individual estimate of cumulative dpm
exposure for each miner in the cohort. Although most cohort members
(including non-drivers) had estimated cumulative exposures less than 1
g-hr/m\3\, some members had cumulative exposures that ranged as high as
11.6 g-hr/m\3\ (ibid., Figure 9.1 and Table 9.1).
    A statistical analysis (time-dependent proportional hazards
regression) was performed to examine the relationship between lung
cancer risk and each miner's estimated cumulative dpm exposure
(unlagged and lagged by 15 years), attained age, smoking habit, mine,
and cohort entry date. Smoking habit was represented by non-smoker, ex-
smoker, and smoker categories, along with the average number of
cigarettes smoked per day for the smokers. Pipe tobacco consumption was
expressed by an equivalent number of cigarettes per day.
    In their written comments, MARG and the NMA both mischaracterized
the results of this study, apparently confusing it with a preliminary
analysis of the same cohort. The preliminary analysis (one part of what
Johnston et al. refer to as the ``wider mortality study'') was
summarized in Section 1.2 (pp 3-5) of the 105-page report at issue,
which may account for the confusion by MARG and the NMA.\50\
---------------------------------------------------------------------------

    \50\ Since MARG and the NMA both stressed the importance of a
quantitative exposure assessment, it is puzzling that they focused
on a crude SMR from the preliminary analysis and ignored the
quantitative results from the subsequent analysis. Johnston et al.
noted that SMRs from the preliminary analysis were consistent ``with
other studies of occupational cohorts where a healthy worker effect
is apparent.'' But even the preliminary analysis explored a possible
surrogate exposure-response relationship, rather than simply relying
on SMRs. Unlike the analysis by Johnston et al., the preliminary
analysis used travel time as a surrogate measure of dpm exposure and
made no attempt to further quantify dpm exposure concentrations.
(ibid.,p.5)
---------------------------------------------------------------------------

    Contrary to the MARG and NMA characterization, Johnston et al.
found a positive, quantitative relationship between cumulative dpm
exposure (lagged by 15 years) and an excess risk of lung cancer, after
controlling for age, smoking habit, and cohort entry date. For each
incremental g-hr/m\3\ of cumulative occupational dpm exposure, the
relative risk of lung cancer was estimated to increase by a factor of
22.7 percent. Adjusting for mine-to-mine differences that may account
for a portion of the elevated risk reduced the estimated RR factor to
15.6 percent. Therefore, with the mine-specific adjustment, the
estimated RR was 1.156 per g-hr/m\3\ of cumulative dpm exposure. It
follows that, based on the mine-adjusted model, the estimated RR for a
specified cumulative exposure is 1.156 raised to a power equal to that
exposure. For example, RR = (1.156)\3.84\ = 1.74 for a cumulative dpm
exposure of 3.84 g-hr/m\3\, and RR = (1.156)\7.68\ = 3.04 for a
cumulative dpm exposure of 7.68 g-hr/m\3\.\51\ Estimates of RR based on
the mine-unadjusted model would substitute 1.227 for 1.156 in these
calculations.
---------------------------------------------------------------------------

    \51\ Assuming an average dpm concentration of 200 g/
m\3\ and 1920 work hours per year, 3.84 g-hr/m\3\ and 7.68 g-hr/m\3\
correspond to 10 and 20 years of occupational exposure,
respectively.
---------------------------------------------------------------------------

    Two limitations of this study weaken the evidence it presents of an
increasing exposure-response relationship. First, although the exposure
assessment is quantitative and carefully done, it is indirect and
depends heavily on assumptions linking surrogate measurements to dpm
exposure levels. The authors, however, analyzed sources of inaccuracy
in the exposure assessment and concluded that ``the similarity between
the estimated * * * [dpm] exposure concentrations derived by the two
different methods give some degree of confidence in the accuracy of the
final values * * *.'' (ibid., pp. 71-75) Second, the highest estimated
cumulative dpm exposures were clustered at a single coal mine, where
the SMR was elevated relative to the regional norm. Therefore, as the
authors pointed out, this one mine greatly influences the results and
is a possible confounder in the study. The investigators also noted
that this mine was ``* * * found to have generally the higher exposures
to respirable quartz and low level radiation.'' Nevertheless, MSHA
regards it likely that the relatively high dpm exposures at this mine
were responsible for at least some of the excess mortality. There is no
apparent way, however, to ascertain just how much of the excess
mortality (including lung cancer) at this coal mine should be
attributed to high occupational dpm exposures and how much to
confounding factors distinguishing it (and the employees working there)
from other mines in the study.
    The RR estimates based on the mine-unadjusted model assume that the
excess lung cancer observed in the cohort is entirely attributable to
dpm exposures, smoking habits, and age distribution. If some of the
excess lung cancer is attributed to other differences between mines,
then the dpm effect is estimated by the lower RR based on the mine-
adjusted model.
    For purposes of comparison with the findings of Saverin et
al.(1999), it will be useful to calculate the RR for a cumulative dpm
exposure of 11.7 g-hr/m\3\ (i.e., the approximate equivalent of 4.9 mg-
yr/m\3\ TC).\52\ At this exposure level, the mine-unadjusted model
produces an estimated RR = (1.227) \11.7\ = 11, and the mine-adjusted
model produces an estimated RR = (1.156) \11.7\ = 5.5.
---------------------------------------------------------------------------

    \52\ This value represents 20 years of cumulative exposure for
the most highly exposed category of workers in the cohort studied by
Saverin et al.
    As explained elsewhere in this preamble, TC constitutes
approximately 80 percent of total dpm. Therefore, the TC value of
4.9 mg-yr/m\3\ presented by Saverin et al. must first be divided by
0.8 to produce a corresponding dpm value of 6.12 mg-yr/m\3\. To
convert this result to the units used by Johnston et al., it is then
multiplied by 1920 work hours per year and divided by 1000 mg/g to
yield 11.7 g-hr/m\3\. This is nearly identical to the maximum
cumulative dpm exposure estimated for locomotive drivers in the
study by Johnston et al. (See Johnston et al., op cit., Table 9.1.)
---------------------------------------------------------------------------

    Saverin et al. (1999) studied a cohort of male potash miners in
Germany who had worked underground for at least one year after 1969,
when the mines involved began converting to diesel powered vehicles and
loading equipment. Members of the cohort were selected based on company
medical records, which also provided bi-annual information on work
location for each miner and, routinely after 1982, the miner's smoking
habits. After excluding miners whose workplace histories could not be
reconstructed from the medical records (5.5 percent) and miners lost to
follow-up (1.9 percent), 5,536 miners remained in the cohort. Within
this full cohort, the authors defined a sub-cohort consisting of 3,258
miners who had ``worked underground for at least ten years, held one
single job during at least 80% of their underground time, and held not
more than three underground jobs in total.''
    The authors divided workplaces into high, medium, and low diesel
exposure categories, respectively corresponding

[[Page 5602]]

to production, maintenance, and workshop areas of the mine. Each of
these three categories was assigned a representative respirable TC
concentration, based on an average of measurements made in 1992. These
averages were 390 g/m\3\ for production, 230 g/m\3\
for maintenance, and 120 g/m\3\ for workshop. Some commenters
expressed concern about using average exposures from 1992 to represent
exposure throughout the study. The authors justified using these
measurement averages to represent exposure levels throughout the study
period because ``the mining technology and the type of machinery used
did not change substantially after 1970.'' This assumption was based on
interviews with local engineers and industrial hygienists.
    Thirty-one percent of the cohort consented to be interviewed, and
information from these interviews was used to validate the work history
and smoking data reconstructed from the medical records. The TC
concentration assigned to each work location was combined with each
miner's individual work history to form an estimate of cumulative
exposure for each member of the cohort. Mean duration of exposure was
15 years. As of the end of follow-up in 1994, average age was 49 years,
average time since first exposure was 19 years, and average cumulative
exposure was 2.70 mg-y/m\3\.
    The authors performed an analysis (within each TC exposure
category) of smoking patterns compared with cumulative TC exposure.
They also analyzed smoking misclassification as estimated by comparing
information from the interviews with medical records. From these
analyses, the authors determined that the cohort was homogeneous with
respect to smoking and that a smoking adjustment was neither necessary
nor desirable for internal comparisons. However, they did not entirely
rule out the possibility that smoking effects may have biased the
results to some extent. On the other hand, the authors concluded that
asbestos exposure was minor and restricted to jobs in the workshop
category, with negligible effects. The miners were not occupationally
exposed to radon progeny, as documented by routine measurement records.
    As compared to the general male population of East Germany, the
cohort SMR for all causes combined was less than 0.6 at a 95-percent
confidence level. The authors interpreted this as demonstrating a
healthy worker effect, noting that ``underground workers are heavily
selected for health and sturdiness, making any surface control group
incomparable.'' Accordingly, they performed internal comparisons within
the cohort of underground miners. The RR reported for lung cancer among
miners in the high-exposure production category, compared to those in
the low-exposure workshop category, was 2.17. The corresponding RR was
not elevated for other cancers or for diseases of the circulatory
system.
    Two statistical methods were used to investigate the relationship
between lung cancer RR and each miner's age and cumulative TC exposure:
Poisson regression and time-dependent proportional hazards regression.
These two statistical methods were applied to both the full cohort and
the subcohort, yielding four different estimates characterizing the
exposure-response relationship. Although a high confidence level was
not achieved, all four of these results indicated that the RR increased
with increasing cumulative TC exposure. For each incremental mg-yr/m\3\
of occupational TC exposure, the relative risk of lung cancer was
estimated to increase by the following multiplicative factor: \53\
---------------------------------------------------------------------------

    \53\ MSHA determined these values by calculating the antilog, to
the base e, of each corresponding estimate of  reported by
Saverin et al. (op cit.) in their Tables III and IV. The cumulative
exposure unit of mg-yr/m \3\ refers to the average TC concentration
experienced over a year's worth of 8-hour shifts.

------------------------------------------------------------------------
                                                       RR per  mg-yr/m3
                                                     -------------------
                       Method                           Full
                                                       cohort  Subcohort
------------------------------------------------------------------------
Poisson.............................................    1.030     1.139
Proportional Hazards................................    1.112     1.225
------------------------------------------------------------------------

    Based on these estimates, the RR for a specified cumulative TC
exposure (X) can be calculated by raising the tabled value to a power
equal to X. For example, using the proportional hazards analysis of the
subcohort, the RR for X = 3.5 mg-yr/m3 is
(1.225)3.5 = 2.03.\54\ The authors calculated the RR
expected for a cumulative TC exposure of 4.9 mg-yr/m3, which
corresponds to 20 years of occupational exposure for miners in the
production category of the cohort. These miners were exposed for five
hours per 8-hour shift at an average TC concentration of 390
g/m3. The resulting RR values were reported as
follows:
---------------------------------------------------------------------------

    \54\ This is the estimated risk relative not to miners in the
workshop category but to a theoretical age-adjusted baseline risk
for cohort members accumulating zero occupational TC exposure.

------------------------------------------------------------------------
                                                      RR for 4.9  mg-yr/
                                                              m3
                       Method                        -------------------
                                                        Full
                                                       cohort  Subcohort
------------------------------------------------------------------------
Poisson.............................................     1.16      1.89
Proportional Hazards................................     1.68      2.70
------------------------------------------------------------------------

    This study has two important limitations that weaken the evidence
it presents of a positive correlation between cumulative TC exposure
and the risk of lung cancer. These are (1) potential confounding due to
tobacco smoking and (2) a significant probability (i.e., greater than
10 percent) that a correlation of the magnitude found could have arisen
simply by chance, given that it were based on a relatively small number
of lung cancer cases.
    Although data on smoking habits were compiled from medical records
for approximately 80 percent of the cohort, these data were not
incorporated into the statistical regression models. The authors
justified their exclusion of smoking from these models by showing that
the likelihood of smoking was essentially unrelated to the cumulative
TC exposure for cohort members. Based on the portion of the cohort that
was interviewed, they also determined that the average number of
cigarettes smoked per day was the same for smokers in the high and low
TC exposure categories (production and workshop, respectively).
However, these same interviews led them to question the accuracy of the
smoking data that had been compiled from medical records. Despite the
cohort's apparent homogeneity with respect to smoking, the authors
noted that smoking was potentially such a strong confounder that ``even
small inaccuracies in smoking data could cause effects comparable in
size to the weak carcinogenic effect of diesel exhaust.'' Therefore,
they excluded the smoking data from the analysis and stated they could
not entirely rule out the possibility of a smoking bias. MSHA agrees
with the authors of this report and the HEI Expert Panel (op cit.) that
even a high degree of cohort homogeneity does not rule out the
possibility of a spurious correlation due to residual smoking effects.
Nevertheless, because of the cohort's homogeneity, the authors
concluded that ``the results are unlikely to be substantially biased by
confounding,'' and MSHA accepts this conclusion.
    The second limitation of this study is related to the fact that the
results are based on a total of only 38 cases of lung cancer for the
full cohort and 21 cases for the subcohort. In their description of
this study at the May 27, 1999, public

[[Page 5603]]

hearing, NIOSH noted that the ``lack of [statistical] significance may
be a result of the study having a small cohort (approximately 5,500
workers), a limited time from first exposure (average of 19 years), and
a young population (average age of 49 years at the end of follow-up).''
More cases of lung cancer may be expected to occur within the cohort as
its members grow older. The authors of the study addressed statistical
significance as follows:

* * * the small number of lung cancer cases produced wide confidence
intervals for all measures of effect and substantially limited the
study power. We intend to extend the follow-up period in order to
improve the statistical precision of the exposure-response
relationship. [Saverin et al., op cit.]

    Some commenters stated that due to these limitations, data from the
Saverin et al. study should not be the basis of this rule. On the other
hand, NIOSH commented that ``[d]espite the limitations discussed * * *
the findings from the Saverin et al. (1999) study should be used as an
alternative source of data for quantifying the possible lung cancer
risks associated with Dpm exposures.'' As stated earlier, MSHA is not
relying on any single study but, instead, basing its evaluation on the
weight of evidence from all available data.
(iii) Best Available Epidemiologic Evidence
    Based on the evaluation criteria described earlier, and after
considering all the public comment that was submitted, MSHA has
identified four cohort studies (including two from U.S.) and four case-
control studies (including three from U.S.) that provide the best
currently available epidemiologic evidence relating dpm exposure to an
increased risk of lung cancer. Three of the 11 studies involving miners
fall into this select group. MSHA considers the statistical
significance of the combined evidence far more important than
confidence levels for individual studies. Therefore, in choosing the
eight most informative studies, MSHA placed less weight on statistical
significance than on the other criteria. The basis for MSHA's selection
of these eight studies is summarized as follows:

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    Six entirely negative studies were identified earlier in this risk
assessment. Several commenters objected to MSHA's treatment of the
negative studies, indicating that they had been discounted without
sufficient justification. To put this in proper perspective, the six
negative studies should be compared to those MSHA has identified as the
best available epidemiologic evidence, with respect to the same
evaluation criteria. (It should be noted that the statistical
significance of a negative study is best represented by its power.) In
accordance with those criteria, MSHA discounts the evidentiary
significance of these six studies for the following reasons:

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[[Page 5606]]

    Other studies proposed as counter-evidence by some commenters will
be addressed in the next subsection of this risk assessment.
    The eight studies MSHA identified as representing the best
available epidemiologic evidence all reported an elevated risk of lung
cancer associated with diesel exposure. The results from these studies
will now be reviewed, along with MSHA's response to public comments as
appropriate.

Boffetta et al., 1988

    The structure of this cohort study was summarized in the preceding
subsection of this risk assessment. The following table contains the
main results. The relative risks listed for duration of exposure were
calculated with reference to all members of the cohort reporting no
diesel exposure, regardless of occupation, and adjusted for age,
smoking pattern, and other occupational exposures (asbestos, coal and
stone dusts, coal tar and pitch, and gasoline exhausts). The relative
risks listed for occupations were calculated for cohort members that
ever worked in the occupation, compared to cohort members never working
in any of the four occupations listed and reporting no diesel exposure.
These four relative risks were adjusted for age and smoking pattern
only. Smoking pattern was coded by 5 categories: never smoker; current
1-20 cigarettes per day; current 21 or more cigarettes per day; ex-
smoker of cigarettes; current or past pipe and/or cigar smoker.

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[[Page 5608]]

    In addition to comments (addressed earlier) on the RR for miners in
this study, IMC Global submitted several comments pertaining to the RR
calculated for persons who explicitly stated that they had been
occupationally exposed to diesel emissions. This RR was 1.18 for
persons reporting any exposure (regardless of duration) compared to all
subjects reporting no exposure. MSHA considers the most important issue
raised by IMC Global to be that 20.6 percent of all cohort members did
not answer the question about occupational diesel exhaust exposure
during their lifetimes, and these subjects experienced a higher age-
adjusted mortality rate than the others. As the authors of this study
acknowledged, this ``could introduce a substantial bias in the estimate
of the association.'' (Boffetta et al., 1988, p.412).
    To show that the impact of this bias could indeed be substantial,
the authors of the study addressed one extreme possibility, in which
all ``unknowns'' were actually unexposed. Under this scenario,
excluding the ``unknowns'' would have biased the calculated RR upward
by a sufficient amount to explain the entire 18-percent excess in RR.
This would not, however, explain the higher RR for persons reporting
more than 16 years exposure, compared to the RR for persons reporting 1
to 15 years. Moreover, the authors did not discuss the opposite
extreme: if all or most of the ``unknowns'' who experienced lung cancer
were actually exposed, then excluding them would have biased the
calculated RR downward. There is little basis for favoring one of these
extremes over the other.
    Another objection to this study raised by IMC Global was:

    All exposure information in the study was self-reported and not
validated. The authors of the study have no quantitative data or
measurements of actual diesel exhaust exposures.

    MSHA agrees with IMC Global and other commenters that a lack of
quantitative exposure measurements limits the strength of the evidence
this study presents. MSHA believes, however, that the evidence
presented is nevertheless substantial. The possibility of random
classification errors due to self-reporting of exposures does not
explain why persons reporting 16 or more years of exposure would
experience a higher relative risk of lung cancer than persons reporting
1 to 15 years of exposure. This difference is not statistically
significant, but random exposure misclassification would tend to make
the effects of exposure less conspicuous. Nor can self-reporting
explain why an elevated risk of lung cancer would be observed for four
occupations commonly associated with diesel exposure.
    Furthermore, the study's authors did perform a rough check on the
accuracy of the cohort's exposure information. First, they confirmed
that, after controlling for age, smoking, and other occupational
exposures, a statistically significant relationship was found between
excess lung cancer and the cohort's self-reported exposures to
asbestos. Second they found no such association for self-reported
exposure to pesticides and herbicides, which they considered unrelated
to lung cancer (ibid., pp. 410-411).
    IMC Global also commented that the ``* * * study may suffer from
volunteer bias in that the cohort was healthier and less likely to be
exposed to important risk factors, such as smoking or alcohol.'' They
noted that this possibility ``is supported by the U.S. EPA in their
draft Health Assessment Document for Diesel Emissions.''
    The study's authors noted that enrollment in the cohort was
nonrandom and that participants tended to be healthier and less exposed
to various risk factors than the general population. These differences,
however, would tend to reduce any relative risk for the cohort
calculated in comparison to the external, general population. The
authors pointed out that external comparisons were, therefore,
inappropriate; but ``the internal comparisons upon which the foregoing
analyses are based are not affected strongly by selection biases.''
(ibid.)
    Although the 1999 EPA draft notes potential volunteer bias, it
concludes: ``Given the fact that all diesel exhaust exposure
occupations * * * showed elevated lung cancer risk, this study is
suggestive of a causal association.'' \55\ (EPA, 1999, p. 7-13) No
objection to this conclusion was raised in the most recent CASAC review
of the EPA draft (CASAC, 2000).
---------------------------------------------------------------------------

    \55\ In his review of this study for the NMA, Dr. Peter Valberg
stated: ``This last sentence reveals EPA's bias; the RRs for truck
drivers and railroad workers were not statistically elevated.''
Contrary to Dr. Valberg's statement, the RRs were greater than 1.0
and, therefore, were ``statistically elevated.'' Although the
elevation for these two occupations was not statistically
significant at a 95-percent confidence level, the EPA made no claim
that it was. Under a null hypothesis of no real association, the
probability should be \1/2\ that the RR would exceed 1.0 for an
occupation associated with diesel exposure. Therefore, under the
null hypothesis, the probability that the RR would exceed 1.0 for
all four such occupations is (1/2) 4 = 0.06. This
corresponds to a 94-percent confidence level for rejecting the null
hypothesis.
---------------------------------------------------------------------------

Boffetta et al., 1990

    This case-control study was based on 2,584 male hospital patients
with histologically confirmed lung cancer, matched with 5099 male
patients with no tobacco-related diseases. Cases and controls were
matched within each of 18 hospitals by age (within two years) and year
of interview. Information on each patient, including medical and
smoking history, occupation, and alcohol and coffee consumption, was
obtained at the time of diagnosis in the hospital, using a structured
questionnaire. For smokers, smoking data included the number of
cigarettes per day. Prior to 1985, only the patient's usual job was
recorded. In 1985, the questionnaire was expanded to include up to five
other jobs and the length of time worked in each job. After 1985,
information was also obtained on dietary habits, vitamin consumption,
and exposure to 45 groups of chemicals, including diesel exhaust.
    The authors categorized all occupations into three groups,
representing low, possible, and probable diesel exhaust exposure. The
``low exposure'' group was used as the reference category for
calculating odds ratios for the ``possible'' and ``probable'' job
groups. These occupational comparisons were based on the full cohort of
patients, enrolled both before and after 1985. A total of 35 cases and
49 controls (all enrolled after the questionnaire was expanded in 1985)
reported a history of diesel exposure. The reference category for self-
reported diesel exposure consisted of a corresponding subset of 442
cases and 897 controls reporting no diesel exposure on the expanded
questionnaire. The authors made three comparisons to rule out bias due
to self-reporting of exposure: (1) No difference was found between the
average number of jobs reported by cases and controls; (2) the
association between self-reported asbestos exposure was in agreement
with previously published estimates; and (3) no association was found
for two exposures (pesticides and fuel pumping) considered unrelated to
lung cancer (ibid., p. 584).
    Stober and Abel (1996) identified this study as being ``of eminent
importance owing to the care taken in including the most influential
confounding factors and analyses of dose-effect relationships.'' The
main findings are presented in the following table. All of these
results were obtained using logistic regression, factoring in the
estimated effects of age, race, years of

[[Page 5609]]

education, number of cigarettes per day, and asbestos exposure (yes or
no). An elevated risk of lung cancer was reported for workers with more
than 30 years of either self-reported or ``probable'' diesel exposure.
The authors repeated the occupational analysis using ``ever'' rather
than ``usual'' employment in jobs classified as ``probable'' exposure,
with ``remarkably similar'' results (ibid., p. 584).

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    The study's authors noted that most U.S. trucks did not have diesel
engines until the late 1950s or early 1960s and that many smaller
trucks are still powered by gasoline engines. Therefore, they performed
a separate analysis of truck drivers cross-classified by self-reported
diesel exposure ``to compare presumptive diesel truck drivers with
nondiesel drivers.'' After adjusting for smoking, the resulting OR for
diesel drivers was 1.25, with a 95-percent confidence interval of 0.85
to 2.76 (ibid., p. 585).

Bruske-Hohlfeld et al., 1999

    This was a pooled analysis of two case-control studies on lung
cancer in Germany. The data pool consisted of 3,498 male cases with
histologically or cytologically confirmed lung cancer and 3,541 male
controls randomly drawn from the general population. Cases and controls
were matched for age and region of residence. For the pooled analysis,
information on demographic characteristics, smoking, and detailed job
and job-task history was collected by personal interviews with the
cases and controls, using a standardized questionnaire.
    Over their occupational lifetimes, cases and controls were employed
in an average of 2.9 and 2.7 different jobs, respectively. Jobs
considered to have had potential exposure to diesel exhaust were
divided into four groups: Professional drivers (including trucks,
buses, and taxis), other ``traffic-related'' jobs (including switchmen
and operators of diesel locomotives or diesel forklift trucks), full-
time drivers of farm tractors, and heavy equipment operators. Within
these four groups, each episode of work in a particular job was
classified as being exposed or not exposed to diesel exhaust, based on
the written description of job tasks obtained during the interview.
This exposure assessment was done without knowledge of the subject's
case or control status. Each subject's lifetime duration of
occupational exposure was compiled using only the jobs determined to
have been diesel-exposed. There were 264 cases and 138 controls who
accumulated diesel exposure exceeding 20 years, with 116 cases and 64
controls accumulating more than 30 years of occupational exposure.
    For each case and control, detailed smoking histories from the
questionnaire were used to establish smoking habit, including
consumption of other tobacco products, cumulative smoking exposure
(expressed as pack-years), and years since quitting smoking. Cumulative
asbestos exposure (expressed as the number of exposed working days) was
assessed based on 17 job-specific questionnaires that supplemented the
main questionnaire.

[[Page 5610]]

    The main findings of this study, all adjusted for cumulative
smoking and asbestos exposure, are presented in the following table.
Although the odds ratio for West German professional drivers was a
statistically significant 1.44, as shown, the odds ratio for East
German professional drivers was not elevated. As a possible
explanation, the authors noted that after 1960, the number of vehicles
(cars, busses, and trucks) with diesel engines per unit area was about
five times higher in West Germany than in East Germany. Also, the
higher OR shown for professional drivers first exposed after 1955,
compared to earlier years of first exposure, may have resulted from the
higher density of diesel traffic in later years.

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[[Page 5612]]

    As the authors noted, a strength of this study is the good
statistical power resulting from having a significant number of workers
exposed to diesel emissions for more than 30 years. Another strength is
the statistical treatment of potential confounders, using quantitative
measures of cumulative smoking and asbestos exposures.
    Although they did not rely solely on job title, and differentiated
between diesel-exposed and unexposed work periods, the authors
identified limitations in the assessment of diesel exposure, ``under
these circumstances leading to an odds ratio that is biased towards one
and an underestimation of the true [relative] risk of lung cancer.'' A
more quantitative assessment of diesel exposure would tend to remove
this bias, thereby further elevating the relative risks. Therefore, the
authors concluded that their study ``showed a statistically significant
increase in lung cancer risk for workers occupationally exposed to
[diesel exhaust] in Germany with the exception of professional drivers
in East Germany.''

Garshick et al., 1987

    This case-control study was based on 1,256 primary lung cancer
deaths and 2,385 controls whose cause of death was not cancer, suicide,
accident, or unknown. Cases and controls were drawn from records of the
U.S. Railroad Retirement Board (RRB) and matched within 2.5 years of
birth date and 31 days of death date. Selected jobs, with and without
regular diesel exposure, were identified by a review of job titles and
duties and classified as ``exposed'' or ``unexposed'' to diesel
exhaust. For 39 jobs, this exposure classification was confirmed by
personal sampling of current respirable dust concentrations, adjusted
for cigarette smoke, at four different railroads. Jobs for which no
personal sampling was available were classified based on similarities
in location and activity to sampled jobs.
    A detailed work history for each case and control was obtained from
an annual report filed with the RRB. This was combined with the
exposure classification for each job to estimate the lifetime total
diesel exposure (expressed as ``diesel-years'') for each subject. Years
spent not working for a railroad, or for which a job was not recorded,
were considered to be unexposed. This amounted to 2.4% of the total
worker-years from 1959 to death or retirement.
    Because of the transition from steam to diesel locomotives in the
1950s, occupational lifetime exposures were accumulated beginning in
1959. Since many of the older workers retired not long after 1959 and
received little or no diesel exposure, separate analyses were carried
out for subjects above and below the age of 65 years at death. The
group of younger workers was considered to be less susceptible to
exposure misclassification.
    Detailed smoking histories, including years smoked, cigarettes per
day, and years between quitting and death, were obtained from next of
kin. Based on job history, each case and control was also classified as
having had regular, intermittent, or no occupational asbestos exposure.
    The main results of this study, adjusted for smoking and asbestos
exposure, are presented in the following table for workers aged less
than 65 years at the time of their death. All of these results were
obtained using logistic regression, conditioned on dates of birth and
death. The odds ratio presented in the shaded cell for 20 years of
unlagged exposure was derived from an analysis that modeled diesel-
years as a continuous variable. All of the other odds ratios in the
table were derived from analyses that modeled cumulative exposure
categorically, using workers with less than five diesel-years of
exposure as the reference group. Statistically significant elevations
of lung cancer risk were reported for the younger workers with at least
20 diesel-years of exposure or at least 15 years accumulated five years
prior to death. No elevated risk of lung cancer was observed for the
older workers, who were 65 or more years old at the time of their
death. The authors attributed this to the fact, mentioned above, that
many of these older workers retired shortly after the transition to
diesel-powered locomotives and, therefore, experienced little or no
occupational diesel exposure. Based on the results for younger workers,
they concluded that ``this study supports the hypothesis that
occupational exposure to diesel exhaust increases lung cancer risk.''

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    In its 1999 draft Health Assessment Document for Diesel Emissions,
the U.S. EPA noted various limitations of this study but concluded that
``compared with previous studies [i.e., prior to 1987] * * *, [it]
provides the most valid evidence that occupational diesel exhaust
emission exposure increases the risk of lung cancer.'' (EPA, 1999, p.
7-33) No objection to this conclusion was raised in the most recent
CASAC review of the EPA draft (CASAC, 2000).
    The EMA objected to this study's determination of smoking frequency
based on interviews with next of kin, stating that such determination
``generally results in an underestimate, as it has been shown that
cigarette companies manufacture 60% more product than public surveys
indicate are being smoked.''
    A tendency to mischaracterize smoking frequency would have biased
the study's reported results if the degree of under- or over-estimation
varied systematically with diesel exposure. The EMA, however, submitted
no evidence that the smoking under-estimate, if it existed at all, was
in any way correlated with cumulative duration of diesel exposure. In
the absence of such evidence, MSHA finds no reason to assume
differential mis-reporting of smoking frequency.
    Even more importantly, the EMA failed to distinguish between
``public surveys'' of the smokers themselves (who may be inclined to
understate their habit) and interviews with next of kin. The
investigators specifically addressed the accuracy of smoking data
obtained from next of kin, citing two studies on the subject. Both
studies reported a tendency for surrogate respondents to overestimate,
rather than underestimate, cigarette consumption. The authors concluded
that ``this could exaggerate the contribution of cigarette smoking to
lung cancer risk if the next of kin of subjects dying of lung cancer
were more likely to report smoking histories than were those of
controls.'' (ibid, p.1246)
    IMC Global, along with Cox (1997) objected to several
methodological features of this study. MSHA's response to each of these
criticisms appears immediately following a summary quotation from IMC
Global's written comments:

    (A) The regression models used to analyze the data assumed
without justification that an excess risk at any exposure level
implied an excess risk at all exposure levels.

    The investigators did not extrapolate their regression models
outside the range supported by the data. Furthermore, MSHA is using
this study only for purposes of hazard identification at exposure
levels at least as high as those experienced by workers in the study.
Therefore, the possibility of a threshold effect at much lower levels
is irrelevant.

    (B) The regression model used did not specify that the exposure
estimates were imperfect surrogates for true exposures. As a result,
the regression coefficients do not bear any necessary relationship
to the effects that they try to measure.

    As noted by Cox (op cit.), random measurement errors for exposures
in an univariate regression model will tend to bias results in the
direction of no apparent association, thereby masking or reducing any
apparent effects of exposure. The crux of Cox's criticism, however, is
that, for statistical analysis

[[Page 5614]]

of the type employed in this study, random errors in a multivariate
exposure (such as an interdependent combination of smoking, asbestos,
and diesel exposure) can potentially bias results in either direction.
This objection fails to consider the fact that a nearly identical
regression result was obtained for the effect of diesel exposure when
smoking and asbestos exposure were removed from the model: OR = 1.39
instead of 1.41. Furthermore, even with a multivariate exposure,
measurement errors in the exposure being evaluated typically bias the
estimate of relative risk downward toward a null result. Relative risk
is biased upwards only when the various exposures are interrelated in a
special way. No evidence was presented that the data of this study met
the special conditions necessary for upward bias or that any such bias
would be large enough to be of any practical significance.

C) The * * * analysis used regression models without presenting
diagnostics to show whether the models were appropriate for the
date.

    MSHA agrees that regression diagnostics are a valuable tool in
assuring the validity of a statistical regression analysis. There is
nothing at all unusual, however, about their not having been mentioned
in the published report of this study. Regression diagnostics are
rarely, if ever, published in epidemiologic studies making use of
regression analysis. This does not imply that such diagnostics were not
considered in the course of identifying an appropriate model or
checking how well the data conform to a given model's underlying
assumptions. Evaluation of the validity of any statistical analysis is
(or should be) part of the peer-review process prior to publication.

D) The * * * risk models assumed that 1959 was the effective year
when DE exposure started for each worker. Thus, the analysis ignored
the potentially large differences in pre-1959 exposures among
workers. This modeling assumption makes it impossible to interpret
the results of the study with confidence.

    MSHA agrees that the lack of diesel exposure information on
individual workers prior to 1959 represents an important limitation of
this study. This limitation, along with a lack of quantitative exposure
data even after 1959, may preclude using it to determine, with
reasonable confidence, the shape or slope of a quantitative exposure-
response relationship. Neither of these limitations, however,
invalidates the study's finding of an elevated lung cancer risk for
exposed workers. MSHA is not basing any quantitative risk assessment on
this study and is relying on it, in conjunction with other evidence,
only for purposes of hazard identification.

E) The risk regression models * * * assume, without apparent
justification, that all exposed individuals have identical dose-
response model parameters (despite the potentially large differences
in their pre-1959 exposure histories). This assumption was not
tested against reasonable alternatives, e.g., that individuals born
in different years have different susceptibilities * * *

    Cases and controls were matched on date of birth to within 2.5
years, and separate analyses were carried out for the two groups of
younger and older workers. Furthermore, it is not true that the
investigators performed no tests of reasonable alternatives even to the
assumption that younger workers shared the same model parameters. They
explored and tested potential interactions between smoking intensity
and diesel exposure, with negative results. The presence of such
interactions would have meant that the response to diesel exposure
differed among individuals, depending on their smoking intensity.
    One other objection that Cox (op. cit.) raised specifically in
connection with this study was apparently overlooked by IMC Global. To
illustrate what he considered to be an improper evaluation of
statistical significance when more than one hypothesis is tested in a
study, Cox noted the finding that for workers aged less than 65 years
at time of death, the odds ratio for lung cancer was significantly
elevated at 20 diesel-years of exposure. He then asserted that this
finding was merely

* * * an instance of a whole family of statements of the form
``Workers who were A years or younger at the time of death and who
were exposed to diesel exhaust for Y years had a significantly
increased relative odds ratios for lung cancer. The probability of
at least one false positive occurring among the multiple hypotheses
in this family corresponding to different combinations of A (e.g.,
no more than 54, 59, 64, 69, 74, 79, etc. years old at death) and
durations of exposure (e.g., Y = 5, 10, 15, 20, 25, etc. years) is
not limited to 5% when each combination of A and Y values is tested
at a p = 5% significance level. For example, if 30 different (A, Y)
combinations are considered, each independently having a 5%
probability of a false positive (i.e., a reported 5% significance
level), then the probability of at least one false positive
occurring in the study as a whole is p = 1 - (1 - 0.05) 30 = 78%.
This p-value for the whole study is more than 15 times greater than
the reported significance level of 5%.

    MSHA is evaluating the cumulative weight of evidence from many
studies and is not relying on the level of statistical significance
attached to any single finding or study viewed in isolation.
Furthermore, Cox's analysis of the statistical impact of multiple
comparisons or hypothesis tests is flawed on several counts, especially
with regard to this study in particular. First, the analysis relies on
a highly unrealistic assumption that when several hypotheses are tested
within the same study, the probabilities of false positives are
statistically independent. Second, Cox fails to distinguish between
those hypotheses or comparisons suggested by exploration of the data
and those motivated by prior considerations. Third, Cox ignores the
fact that the result in question was based on a statistical regression
analysis in which diesel exposure duration was modeled as a single
continuous variable. Therefore, this particular result does not depend
on multiple hypothesis-testing with respect to exposure duration.
Fourth, and most importantly, Cox assumes that age and exposure
duration were randomly picked for tested from a pool of interchangeable
possibilities and that the only thing distinguishing the combination of
``65 years of age'' and ``20 diesel-years of exposure'' from other
random combinations was that it happened to yield an apparently
significant result. This is clearly not the case. The investigators
divided workers into only two age groups and explained that this
division was based on the history of dieselization in the railroad
industry--not on the results of their data analysis. Similarly, the
result for 20 diesel-years of exposure was not favored over shorter
exposure times simply because 20 years yielded a significant result and
the shorter times did not. Lengthy exposure and latency periods are
required for the expression of increased lung cancer risks, and this
justifies a focus on the longest exposure periods for which sufficient
data are available.

Garshick et al., 1988; Garshick, 1991

    In this study, the investigators assessed the risk of lung cancer
in a cohort of 55,407 white male railroad workers, aged 40 to 64 years
in 1959, who had begun railroad work between 1939 and 1949 and were
employed in one of 39 jobs later surveyed for exposure. Workers whose
job history indicated likely occupational exposure to asbestos were
excluded. Based on the subsequent exposure survey, each of the 39 jobs
represented in the cohort was classified as either exposed or unexposed
to diesel emissions. The cohort was followed through 1980, and

[[Page 5615]]

1,694 cases of death due to lung cancer were identified.
    As in the 1987 study by the same investigators, detailed railroad
job histories from 1959 to date of death or retirement were obtained
from RRB records and combined with the exposure classification for each
job to provide the years of diesel exposure accumulated since 1959 for
each worker in the cohort. Using workers classified as ``unexposed''
within the cohort to establish a baseline, time-dependent proportional
hazards regression models were employed to evaluate the relative risk
of lung cancer for exposed workers. Although the investigators believed
they had excluded most workers with significant past asbestos exposures
from the cohort, based on job codes, they considered it possible that
some workers classified as hostlers or shop workers may have been
included in the cohort even if occupationally exposed to asbestos.
Therefore, they carried out statistical analyses with and without shop
workers and hostlers included.
    The main results of this study are presented in the following
table. Statistically significant elevations of lung cancer risk were
found regardless of whether or not shop workers and hostlers were
included. The 1988 analysis adjusted for age in 1959, and the 1991
analysis adjusted, instead, for age at death or end of follow-up (i.e.,
end of 1980).\56\ In the 1988 analysis, any work during a year counted
as a diesel-year if the work was in a diesel-exposed job category, and
the results from the 1991 analysis presented here are based on this
same method of compiling exposure durations. Exposure durations
excluded the year of death and the four prior years, thereby allowing
for some latency in exposure effects. Results for the analysis
excluding shop workers and hostlers were not presented in the 1991
report, but the report stated that ``similar results were obtained.''
Using either method of age adjustment, a statistically significant
elevation of lung cancer risk was associated with each exposure
duration category. Using ``attained age,'' however, there was no strong
indication that risk increased with increasing exposure duration. The
1991 report concluded that ``there appears to be an effect of diesel
exposure on lung cancer mortality'' but that ``because of weaknesses in
exposure ascertainment * * *, the nature of the exposure-response
relationship could not be found in this study.''

    \56\ Also, the 1991 analysis excluded 12 members of the cohort
due to discrepancies between work history and reported year of
death, leaving 55,395 railroad workers included in the analysis.
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    Some commenters noted that removing the shop workers and hostlers
from the analysis increased the relative risk estimates. Dr. Peter
Valberg found this ``paradoxical,'' since workers in these categories
had later been found to experience higher average levels of diesel
exposure than other railroad workers.

    This so-called paradox is likely to have resulted simply from
exposure misclassification for a significant portion of the shop
workers. The effect was explained by Garshick (1991) as follows:

[[Page 5616]]

* * * shop workers who worked in the diesel repair shops shared job
codes with workers in non-diesel shops where there was no diesel
exhaust * * *. Apparent exposure as a shop worker based on the job
code was then diluted with workers with the same job code but
without true exposure, making it less likely to see an effect in the
shop worker group. In addition, workers in the shop worker group of
job codes tended to have less stable career paths * * * compared to
the other diesel exposure categories.

    So although many of the shopworkers may have been exposed to
relatively high dpm concentrations, many others were among the lowest-
exposed workers or were even unexposed because they spent their entire
occupational lifetimes in unexposed locations. This could readily
account for the increase in relative risks calculated when shop workers
were excluded from the analysis.
    Dr. Valberg also noted that, according to Crump 1999), mortality
rates for cirrhosis of the liver and heart disease were significantly
elevated for ``train riders,'' who were exposed to diesel emissions, as
compared to other members of the cohort, who were less likely to be
exposed. It is also the train riders who account, primarily, for the
elevated risk of lung cancer associated with diesel exposure in the
overall cohort. Dr. Valberg interpreted this as suggesting that
``lifestyle'' factors such as diet or smoking habits, rather than
diesel exposure, were responsible for the increased risk of lung cancer
observed among the diesel-exposed workers.
    Dr. Valberg presented no evidence that, apart from diesel exposure,
the train riders differed systematically from the other workers in
their smoking habits or in other ways that would be expected to affect
their risk of lung cancer. Therefore, MSHA views the suggestion of such
a bias as speculative. Even if lifestyle factors associated with train
ridership were responsible for an increased risk of cirrhosis of the
liver or heart disease, this would not necessarily mean that the same
factors were also responsible for the increased risk of lung cancer.
Still, it is hypothetically possible that systematic differences, other
than diesel exposure, between train riders and other railroad workers
could account for some or even all of the increased lung cancer risk.
That is why MSHA does not rely on this, or any other, single study in
isolation.
    Some commenters, including the NMA, objected to this study on
grounds that it failed to control for potentially confounding factors,
principally smoking. The NMA stated that this ``has rendered its
utility questionable at best.'' As explained earlier, there is more
than one way in which a study can control for smoking or other
potential confounders. One of the ways is to make sure that groups
being compared do not differ with respect to the potential confounder.
In this study, workers with likely asbestos exposure were excluded from
the cohort, stability of workers within job categories was well
documented, and similar results were reported when job categories
subject to asbestos exposure misclassification were excluded. In their
1988 report, the investigators provided the following reasons to
believe that smoking did not seriously affect their findings:

    * * * the cohort was selected to include only blue-collar
workers of similar socioeconomic class, a known correlate of
cigarette smoking * * *, in our case-control study [Garshick et
al.,1987], when cigarette smoking was considered, there was little
difference in the crude or adjusted estimates of diesel exhaust
effects. Finally, in the group of 517 current railroad workers
surveyed by us in 1982 * * *, we found no difference in cigarette
smoking prevalence between workers with and without potential diesel
exhaust exposure. [Garshick et al.,1988]

    Since relative risks were based on internal comparisons, and the
cohort appears to have been fairly homogeneous, MSHA regards it as
unlikely that the association of lung cancer with diesel exposure in
this study resulted entirely from uncontrolled asbestos or smoking
effects. Nevertheless, MSHA recognizes that differential smoking
patterns may have affected, in either direction, the degree of
association reported in each of the exposure duration categories.
    Cox (1997) re-analyzed the data of this study using exploratory,
nonparametric statistical techniques. As quoted by IMC Global, Cox
concluded that ``these methods show that DE [i.e., dpm] concentration
has no positive causal association with lung cancer mortality risk.''
MSHA believes this quotation (taken from the abstract of Cox's article)
overstates the findings of his analysis. At most, Cox confirmed the
conclusion by Garshick (1991) that these data do not support a positive
exposure-response relationship. Specifically, Cox determined that
inter-relationships among cumulative diesel exposure, age in 1959, and
retirement year make it ``impossible to prove causation by eliminating
plausible rival hypotheses based on this dataset.'' (Cox, 1997; p.826)
Even if Cox's analysis were correct, it would not follow that there is
no underlying causal connection between dpm exposure and lung cancer.
It would merely mean that the data do not contain internal evidence
implicating dpm exposure as the cause, rather than one or more of the
variables with which exposure is correlated. Cox presented no evidence
that any ``rival hypotheses'' were more plausible than causation by dpm
exposure. Furthermore, it may simply be, as Garshick suggested, that an
underlying exposure-response relationship is not evident ``because of
weaknesses in exposure ascertainment.'' (Garshick, 1991, op cit.) None
of this negates the fact that, after adjusting for either age in 1959
or ``attained'' age, lung cancer was significantly more prevalent among
the exposed workers.
    Along similar lines, many commenters pointed out that an HEI expert
panel examined the data of this study (HEI, 1999) and found that it had
very limited use for quantitative risk assessment (QRA). Several of
these commenters mischaracterized the panel's findings. The NMA, for
example, drew the following unjustified conclusion from the panel's
report: ``In short, * * * the correct interpretation of the Garshick
study is that any occupational increase in lung cancer among train
workers was not due to diesel exposures.''
    Contrary to the NMA's characterization, the HEI Expert Panel's
report stated that the data are

* * * consistent with findings of a weak association between death
from lung cancer and occupational exposure to diesel exhaust.
Although the secondary exposure-response analyses * * * are
conflicting, the overall risk of lung cancer was elevated among
diesel-exposed workers. [ibid., p.25]

    The panel agreed with Garshick (1991) and Cox (1997) that the data
of this study do not support a positive exposure-response relationship.
Like Garshick and unlike Cox, however, the panel explicitly recognized
that problems with the data could mask such a relationship and that
this does not negate the statistically significant finding of elevated
risk among exposed workers. Indeed, the panel even identified several
factors, in addition to weak exposure assessment as suggested by
Garshick, that could mask a positive relationship: unmeasured
confounding variables such as cigarette smoking, previous occupational
exposures, or other sources of pollution; a ``healthy worker survivor
effect''; and differential misclassification or incomplete
ascertainment of lung cancer deaths. (HEI, 1999; p.32)
    Positive exposure-response relationships based on these data were
reported by the California EPA (OEHHA, 1998). MSHA recognizes that
those findings were sensitive to various assumptions and that other
investigators

[[Page 5617]]

have obtained contrary results. The West Virginia Coal Association,
paraphrasing Dr. Peter Valberg, concluded that although the two studies
by Garshick et al. `` * * * may represent the best in the field, they
fail to firmly support the proposition that lung cancer risk in workers
derives from exposure to dpm.'' At least one commenter (IMC Global)
apparently reached a considerably stronger conclusion that they were of
no value whatsoever, and urged MSHA to ``discount their results and not
consider them in this rulemaking.'' On the other hand, in response to
the ANPRM, a consultant to the National Coal Association who was
critical of all other studies available at the time acknowledged that
these two:

* * * have successfully controlled for severally [sic] potentially
important confounding factors * * * Smoking represents so strong a
potential confounding variable that its control must be nearly
perfect if an observed association between cancer and diesel exhaust
is * * * [inferred to be causal]. In this regard, two observations
are relevant. First, both case-control [Garshick et al., 1987] and
cohort [Garshick et al., 1988] study designs revealed consistent
results. Second, an examination of smoking related causes of death
other than lung cancer seemed to account for only a fraction of the
association observed between diesel exposure and lung cancer. A high
degree of success was apparently achieved in controlling for smoking
as a potentially confounding variable. [Robert A. Michaels, RAM TRAC
Corporation, submitted by National Coal Association].

    To a limited extent, MSHA agrees with Dr. Valberg and the West
Virginia Coal Association: these two studies--like every real-life
epidemiologic study--are not ``firmly'' conclusive when viewed in
isolation. Nevertheless, MSHA believes that they provide important
contributions to the overall body of evidence. Whether or not they can
be used to quantify an exposure-response relationship, these studies--
among the most comprehensive and carefully controlled currently
available--do show statistically significant increases in the risk of
lung cancer among diesel-exposed workers.

Johnston et al. (1997)

    Since it focused on miners, this study has already been summarized
and discussed in the previous subsection of this risk assessment. The
main results are presented in the following table. The tabled relative
risk estimates presented for cumulative exposures greater than 1000 mg-
hr/m3 (i.e., 1 g-hr/m3) were calculated by MSHA
based on the regression coefficients reported by the authors. The
conversion from mg-hr/m3 to mg-yr/m3 assumes
1,920 occupational exposure hours per year. Although 6.1 mg-yr/
m3 Dpm roughly equals the cumulative exposure estimated for
the most highly exposed locomotive drivers in the study, the relative
risk associated with this exposure level is presented primarily for
purposes of comparison with findings of Saverin et al. (1999).

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    In its post-hearing comments, MARG acknowledged that this study
``found a `weak association' between lung cancer and respiratory diesel
particulate exposure'' but failed to note that the estimated relative
risk increased with increasing exposure. MARG also stated that the
association was ``deemed non-significant by the researchers'' and that
``no association was found among men with different exposures working
in the same mines.'' Although the mine-adjusted model did not support
95-percent confidence for an increasing exposure-response relationship,
the mine-unadjusted model yielded a statistically significant positive
slope at this confidence level. Furthermore, since the mine-adjusted
model adjusts for differences in lung cancer rates between mines, the
fact that relative risk increased with increasing exposure under this
model indicates (though not at a 95-percent confidence level) that the
risk of lung cancer increased with exposure among men with different
exposures working in the same mines.

Saverin et al. (1999)

    Since this study, like the one by Johnston et al., was carried out
on a cohort of miners, it too was summarized and discussed in the
previous subsection of this risk assessment. The main results are
presented in the following table. The relative risk estimates and
confidence intervals at the mean exposure level of 2.7 mg-yr/
m3 TC (total carbon) were calculated by MSHA, based on
values of  and corresponding confidence intervals presented in
Tables III and IV of the

[[Page 5618]]

published report (ibid., p.420). The approximate equivalency between
4.9 mg-yr/m3 TC and 6.1 mg-yr/m3 dpm assumes
that, on average, TC comprises 80 percent of dpm.

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    These results are not statistically significant at the conventional
95-percent confidence level. However, the authors noted that the
relative risk calculated for the subcohort was consistently higher than
that calculated for the full cohort. They also considered the subcohort
to have a superior exposure assessment and a better latency allowance
than the full cohort. According to the authors, these factors provide
``some assurance that the observed risk elevation was not entirely due
to chance since improving the exposure assessment and allowing for
latency effects should, in general, enhance exposure effects.''

Steenland et al., (1990, 1992, 1998)

    The basis for the analyses in this series was a case-control study
comparing the risk of lung cancer for diesel-exposed and unexposed
workers who had belonged to the Teamsters Union for at least twenty
years (Steenland et al., 1990). Drawing from union records, 996 cases
of lung cancer were identified among more than 10,000 deaths in 1982
and 1983. For comparison to these cases, a total of 1,085 controls was
selected (presumably at random) from the remaining deaths, restricted
to those who died from causes other than lung cancer, bladder cancer,
or motor vehicle accident. Information on work history, duration and
intensity of cigarette smoking, diet, and asbestos exposure was
obtained from next of kin. Detailed work histories were also obtained
from pension applications on file with the Teamsters Union.
    Both data sources were used to classify cases and controls
according to a job category in which they had worked the longest. Based
on the data obtained from next of kin, the job categories were diesel
truck drivers, gasoline truck drivers, drivers of both truck types,
truck mechanics, and dock workers. Based on the pension applications,
the principal job categories were long-haul drivers, short-haul or city
drivers, truck mechanics, and dock workers. Of the workers identified
by next of kin as primarily diesel truck drivers, 90 percent were
classified as long-haul drivers according to the Teamster data. The
corresponding proportions were 82 percent for mechanics and 81 percent
for dock workers. According to the investigators, most Teamsters had
worked in only one exposed job category. However, because of the
differences in job category definitions, and also because the next of
kin data covered lifetimes whereas the pension applications covered
only time in the Teamsters Union, the investigators found it
problematic to fully evaluate the concordance between the two data
sources.
    In the 1990 report, separate analyses were conducted for each
source of data used to compile work histories. The investigators noted
that ``many trucking companies (where most study subjects worked) had
completed most of the dieselization of their fleets by 1960, while
independent drivers and nontrucking firms may have obtained diesel
trucks later. * * * '' Therefore, they specifically checked for
associations between increased risk of lung cancer and occupational
exposure after 1959 and, separately, after 1964. In the 1992 report,
the investigators presented, for the Union's occupational categories
used in the study, dpm exposure estimates based on subsequent
measurements of submicrometer elemental carbon (EC) as reported by
Zaebst et al. (1991). In the 1998 report, cumulative dpm exposure
estimates for individual workers were compiled by combining the
individual work histories obtained from the Union's records with the
subsequently measured occupational exposure levels, along with an
evaluation of historical changes in diesel engine emissions and
patterns of diesel usage. Three alternative sets of cumulative exposure
estimates were considered, based on alternative assumptions about the
extent of

[[Page 5619]]

improvement in diesel engine emissions between 1970 and 1990. A variety
of statistical models and techniques were then employed to investigate
the relationship between estimated cumulative dpm exposure (expressed
as EC) and the risk of lung cancer. The authors pointed out that the
results of these statistical analyses depended heavily on ``very broad
assumptions'' used to generate the estimates of cumulative dpm
exposure. While acknowledging this limitation, however, they also
evaluated the sensitivity of their results to various changes in their
assumptions and found these changes to have little impact on the
results.
    The investigators also identified and addressed several other
limitations of this study as follows:

    (1) possible misclassification smoking habits by next of kin,
(2) misclassification of exposure by next of kin, (3) a relatively
small non-exposed group (n = 120) which by chance may have had a low
lung cancer risk, and (4) lack of sufficient latency (time since
first exposure) to observe a lung cancer excess. On the other hand,
next-of-kin data on smoking have been shown to be reasonably
accurate, non-differential misclassification of exposure * * * would
only bias our findings toward * * * no association, and the trends
of increased risk with increased duration of employment in certain
jobs would persist even if the non-exposed group had a higher lung
cancer risk. Finally, the lack of potential latency would only make
any positive results more striking. (Steenland et al., 1990)

    The main results from the three reports covering this study are
summarized in the following table. All of the analyses were controlled
for age, race, smoking (five categories), diet, and asbestos exposure
as reported by next of kin. Odds ratios for the occupations listed were
calculated relative to the odds of lung cancer for occupations other
than truck driver (all types), mechanic, dock worker, or other
potentially diesel exposed jobs (Steenland et al., 1990, Appendix A).
The exposure-response analyses were carried out using logistic
regression. Although the investigators performed analyses under three
different assumptions for the rate of engine emissions (gm/mile) in
1970, they considered the intermediate value of 4.5 gm/mile to be their
best estimate, and this is the value on which the results shown here
are based. Under this assumption, cumulative occupational EC exposure
for all workers in the study was estimated to range from 0.45 to 2,440
g-yr/m\3\, with a median value of 373 g-yr/m\3\. The
estimates of relative risk (expressed as odds ratios) presented for EC
exposures of 373 g-yr/m\3\, 1000 g-yr/m\3\, and 2450
-yr/m\3\ were calculated by MSHA based on the regression
coefficients reported by the authors for five-year lagged exposures
(Steenland et al. 1998, Table II).

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[[Page 5620]]

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[[Page 5621]]

    Under the assumption of a 4.5 gm/mile emissions rate in 1970, the
cumulative EC exposure of 2450 g-yr/m\3\ ( 6.1 mg-
yr/m\3\ Dpm) shown in the table closely corresponds to the upper limit
of the range of data on which the regression analyses were based
(Steenland et al., 1998, p. 224). However, the relative risks (i.e.,
odds ratios) calculated for this level of occupational exposure are
presented primarily for purposes of comparison with the findings of
Johnston et al. (1997) and Saverin et al. (1999). At a cumulative Dpm
exposure of approximately 6.1 mg--yr/m\3\, it is evident that the
Johnston models predict a far greater elevation in lung cancer risk
than either the Saverin or Steenland models. A possible explanation for
this is that the Johnston data included exposures of up to 30 years in
duration, and the statistical models showing an exposure-response
relationship allowed for a 15-year lag in exposure effects. The other
two studies were based on generally shorter diesel exposures and
allowed less time for latent effects. In Subsection 3.b.ii(3) of this
risk assessment, the quantitative results of these three studies will
be further compared with respect to exposure levels found in
underground mines.
    Several commenters noted that the HEI Expert Panel (HEI, 1999) had
identified uncertainties in the diesel exposure assessment as an
important limitation of the exposure-response analyses by Steenland et
al. (1998) and had recommended further investigation before the
quantitative results of this study were accepted as conclusive. In
addition, Navistar International Transportation (NITC) raised a number
of objections to the methods by which diesel exposures were estimated
for the period between 1949 and 1990 (NITC, 1999). In general, the
thrust of these objections was that exposures to diesel engine
emissions had been overestimated, while potentially relevant exposures
to gasoline engine emissions had been underestimated and/or unduly
discounted.\57\
---------------------------------------------------------------------------

    \57\ Many of the issues NITC raised in its critique of this
study depend on a peculiar identification of Dpm exclusively with
elemental carbon. For example, NITC argued that ``more than 65
percent of the total carbon to which road drivers (and mechanics)
were exposed consisted of organic (i.e., non-diesel) carbon, further
suggesting that some other etiology caused or contributed to excess
lung cancer mortality in these workers.'' (NITC, 1999, p. 16) Such
lines of argument, which depend on identifying organic carbon as
``non-diesel,'' ignore the fact that Dpm contains a large measure of
organic carbon compounds (and also some sulfates), as well as
elemental carbon. Any adverse health effects due to the organic
carbon or sulfate constituents of Dpm would nonetheless be due to
Dpm exposures.
---------------------------------------------------------------------------

    As mentioned above, the investigators recognized that these
analyses rely on ``broad assumptions rather than actual [concurrent]
measurements,'' and they proposed that the ``results should be regarded
with appropriate caution.'' While agreeing with both the investigators
and the HEI Expert Panel that these results should be interpreted with
appropriate caution, MSHA also agrees with the Panel ``* * * that
regulatory decisions need to be made in spite of the limitations and
uncertainties of the few studies with quantitative data currently
available.'' (HEI, 1999, p. 39) In this context, MSHA considers it
appropriate to regard the 1998 exposure-response analyses as
contributing to the weight of evidence that dpm exposure increases the
risk of lung cancer, even if the results are not conclusive when viewed
in isolation.
    Some commenters also noted that the HEI Expert Panel raised the
possibility that the method for selecting controls in this study could
potentially have biased the results in an unpredictable direction. Such
bias could have occurred because deaths among some of the controls were
likely due to diseases (such as cardiovascular disease) that shared
some of the same risk factors (such as tobacco smoking) with lung
cancer. The Panel presented hypothetical examples of how this might
bias results in either direction. Although the possibility of such bias
further demonstrates why the results of this study should be regarded
with ``appropriate caution,'' it is important to distinguish between
the mere possibility of a control-selection bias, evidence that such a
bias actually exists in this particular study, and the further evidence
required to show that such bias not only exists but is of sufficient
magnitude to have produced seriously misleading results. Unlike the
commenters who cited the HEI Expert Panel on this issue, the Panel
itself clearly drew this distinction, stating that ``no direct evidence
of such bias is apparent'' and emphasizing that ``even though these
examples [presented in HEI (1999), Appendix D] could produce misleading
results, it is important to note that they are only hypothetical
examples. Whether or not such bias is present will require further
examination.'' (HEI, 1999, pp. 37-38) As the HEI showed in its
examples, such bias (if it exists) could lead to underestimating the
association between lung cancer and dpm exposure, as well as to
overestimating it. Therefore, in the absence of evidence that control-
selection bias actually distorted the results of this study one way or
the other, MSHA considers it prudent to accept the study's finding of
an association at face value.
    One commenter (MARG) noted that information on cigarette smoking,
asbestos exposure, and diet in the trucking industry study was obtained
from next of kin and stated that such information was ``likely to be
unreliable.'' By increasing random variability in the data, such errors
could widen the confidence intervals around an estimated odds ratio or
reduce the confidence level at which a positive exposure-response
relationship might be established. However, unless such errors were
correlated with diesel exposure or lung cancer in such a way as to bias
the results, they would not, on average, inflate the estimated degree
of association between diesel exposure and an increased risk of lung
cancer. The commenter provided no reason to suspect that errors with
respect to these factors were in any way correlated with diesel
exposure or with the development of lung cancer.
    Some commenters pointed out that EC concentrations measured in 1990
for truck mechanics were higher, on average, than for truck drivers,
but the mechanics, unlike the drivers, showed no evidence of increasing
lung cancer risk with increasing duration of employment. NITC referred
to this as a ``discrepancy'' in the data, assuming that ``cumulative
exposure increases with duration of employment such that mechanics who
have been employed for 18 or more years would have greater cumulative
exposure than workers who have been employed for 1-11 years.'' (NITC,
1999)
    Mechanics were included in the logistic regression analyses
(Steenland et al., 1998) showing an increase in lung cancer risk with
increasing cumulative exposure. These analyses pooled the data for all
occupations by estimating exposure for each worker based on the
worker's occupation and the particular years in which the worker was
employed. There are at least three reasons why, for mechanics viewed as
a separate group, an increase in lung cancer risk with increasing dpm
exposure may not have been reflected by increasing duration of
employment.
    First, relatively few truck mechanics were available for analyzing
the relationship between length of employment and the risk of lung
cancer. Based on the union records, 50 cases and 37 controls were so
classified; based on the next-of-kin data, 43 cases and 41 controls
were more specifically classified as diesel truck mechanics

[[Page 5622]]

(Steenland et al., 1990). In contrast, 609 cases and 604 controls were
classified as long-haul drivers (union records). This was both the
largest occupational category and the only one showing statistically
significant evidence of increasing risk with increasing employment
duration. The number of mechanics included in the study population may
simply not have been sufficient to detect a pattern of increasing risk
with increasing length of employment, even if such a pattern existed.
    The second part of the explanation as to why mechanics did not
exhibit a pattern similar to truck drivers could be that the data on
mechanics were more subject to confounding. After noting that ``the
risk for mechanics did not appear to increase consistently with
duration of employment,'' Steenland et al. (1990) further noted that
the mechanics may have been exposed to asbestos when working on brakes.
The data used to adjust for asbestos exposure may have been inadequate
to control for variability in asbestos exposure among the mechanics.
    Third, as noted by NITC, the lung cancer risk for mechanics
(adjusted for age, race, tobacco smoking, asbestos exposure, and diet)
would be expected to increase with increasing duration of employment
only if the mechanics' cumulative dpm exposure corresponded to the
length of their employment. None of the commenters raising this issue,
however, provided any support for this assumption, which fails to
consider the particular calendar years in which mechanics included in
the study were employed. In compiling cumulative exposure for an
individual worker, the investigators took into account historical
changes in both diesel emissions and the proportion of trucks with
diesel engines--so the exposure level assigned to each occupational
category was not the same in each year. In general, workers included in
the study neither began nor ended their employment in the same year.
Consequently, workers with the same duration of employment in the same
occupational category could be assigned different cumulative exposures,
depending on when they were employed. Similarly, workers in the same
occupational category who were assigned the same cumulative exposure
may not have worked the same length of time in that occupation.
Therefore, it should not be assumed that duration of employment
corresponds very well to the cumulative exposure estimated for workers
within any of the occupational categories. Furthermore, in the case of
mechanics, there is an additional historical variable that is
especially relevant to actual cumulative exposure but was not
considered in formulating exposure estimates: the degree of ventilation
or other means of protection within repair shops. Historical changes in
shop design and work practices, as well as differences between shops,
may have caused more exposure misclassification among mechanics than
among long-haul or diesel truck drivers. Such misclassification would
tend to further obscure any relationship between mechanics' risk of
lung cancer and either duration of employment or cumulative exposure.
(iv) Counter-Evidence
    Several commenters stated that, in the proposal, MSHA had dismissed
or not adequately addressed epidemiology studies showing no association
between lung cancer and exposures to diesel exhaust. For example, the
EMA wrote:

    MSHA's discussion of the negative studies generally consists of
arguments to explain why those studies should be dismissed. For
example, MSHA states that, ``All of the studies showing negative or
statistically insignificant positive associations * * * lacked good
information about dpm exposure * * *'' or showed similar
shortcomings. 63 Fed. Reg. at 17533. The statement about exposure
information is only partially true, for, in fact, very few of any of
the cited studies (the ``positive'' studies as well) included any
exposure measurements, and none included concurrent exposures.

    It should, first of all, be noted that the statement in question on
dpm exposure referred to the issue of any diesel exposure--not to
quantitative exposure measurements, which MSHA acknowledges are lacking
in most of the available studies. In the absence of quantitative
measurements, however, studies comparing workers known to have been
occupationally exposed to unexposed workers are preferable to studies
not containing such comparisons. Furthermore, two of the studies now
available (and discussed above) utilize essentially concurrent exposure
measurements, and both show a positive association (Johnston et al.,
1997; Saverin et al., 1999).
    MSHA did not entirely ``dismiss'' the negative studies. They were
included in both MSHA's tabulation (see Tables III-4 and III-5) and (if
they met the inclusion criteria) in the two meta-analyses cited both
here and in the proposal (Lipsett and Campleman, 1999, and Bhatia et
al., 1998). As noted by the commenter, MSHA presented reasons (such as
an inadequate latency allowance) for why negative studies may have
failed to detect an association. Similarly MSHA gave reasons for giving
less weight to some of the positive studies, such as Benhamou et al.
(1988), Morabia et al. (1992), and Siemiatycki et al., 1988. Additional
reasons for giving less weight to the six entirely negative studies
have been tabulated above, under the heading of ``Best Available
Epidemiologic Evidence.'' The most recent of these negative studies
(Christie et al., 1994, 1995) is discussed in detail under the heading
of ``Studies Involving Miners.''
    One commenter (IMC Global) listed the following studies (all of
which MSHA had considered in the proposed risk assessment) as
``examples of studies that reported negative associations between [dpm]
exposure and lung cancer risk'':
     Waller (1981). This is one of the six negative studies
discussed earlier. Results were likely to have been biased by excluding
lung cancers occurring after retirement or resignation from employment
with the London Transit Authority. Comparison was to a general
population, and there was no adjustment for a healthy worker effect.
Comparison groups were disparate, and there was no adjustment for
possible differences in smoking frequency or intensity.
     Howe et al. (1983). Contrary to the commenter's
characterization of this study, the investigators reported
statistically significant elevations of lung cancer risk for workers
classified as ``possibly exposed'' or ``probably exposed'' to diesel
exhaust. MSHA recognizes that these results may have been confounded by
asbestos and coal dust exposures.
     Wong et al. (1985). The investigators reported a
statistically insignificant deficit for lung cancer in the entire
cohort and a statistically significant deficit for lung cancer in the
less than 5-year duration group. However, since comparisons were to a
general population, these deficits may be the result of a healthy
worker effect, for which there was no adjustment. Because of the
latency required for development of lung cancer, the result for ``less
than 5-year duration'' is far less informative than the results for
longer durations of employment and greater latency allowances. Contrary
to the commenter's characterization of this study, the investigators
reported statistically significant elevations of lung cancer risks for
``normal'' retirees (SMR = 1.30) and for ``high exposure'' dozer
operators with 15-19 years of union membership and a latency allowance
of at least 20 years (SMR = 3.43).
     Edling et al. (1987). This is one of the six negative
studies discussed

[[Page 5623]]

earlier. The cohort consisted of only 694 bus workers and, therefore,
lacked statistical power. Furthermore, comparison was to a general,
external population with no adjustment for a healthy worker effect.
     Garshick (1988). The reason the commenter (IMC Global)
gave for characterizing this study as negative was: ``That the sign of
the association in this data set changes based on the models used
suggests that the effect is not robust. It apparently reflects modeling
assumptions more than data.'' Contrary to the commenter's
characterization, however, the finding of increased lung cancer risk
for workers classified as diesel-exposed did not change when different
methods were used to analyze the data. What changed, depending on
modeling assumptions, was the shape and direction of the exposure-
response relationship among exposed workers (Cal-EPA, 1998; Stayner et
al., 1998; Crump, 1999; HEI, 1999). MSHA agrees that the various
exposure-response relationships that have been derived from this study
are highly sensitive to data modeling assumptions. This includes
assumptions about historical patterns of exposure, as well as
assumptions related to technical aspects of the statistical analysis.
However, as noted by the HEI Expert Panel, the study provides evidence
of a positive association between exposure and lung cancer despite the
conflicting exposure-response analyses. Even though different
assumptions and methods of analysis have led to different conclusions
about the utility of this study for quantifying an exposure-response
relationship, ``the overall risk of lung cancer was elevated among
diesel-exposed workers'' (HEI, 1999, p. 25).
    Another commenter (MARG) cited a number of studies (all of which
had already been placed in the public record by MSHA) that, according
to the commenter, ``reflect either negative health effects trends among
miners or else failed to demonstrate a statistically significant
positive trend correlated with dpm exposure.'' It should be noted that,
as explained earlier, failure of an individual study to achieve
statistical significance (i.e., a high confidence level for its
results) does not necessarily prevent a study from contributing
important information to a larger body of evidence. An epidemiologic
study may fail to achieve statistical significance simply because it
did not involve a sufficient number of subjects or because it did not
allow for an adequate latency period. In addition to this general
point, the following responses apply to the specific studies cited by
the commenter.
     Ahlman et al. (1991). This study is discussed above, under
the heading of ``Studies Involving Miners.'' MSHA agrees with the
commenter that this study did not ``establish'' a relationship between
diesel exposure and the excess risk of lung cancer reported among the
miners involved. Contrary to the commenter's characterization, however,
the evidence presented by this study does incrementally point in the
direction of such a relationship. As mentioned earlier, none of the
underground miners who developed lung cancer had been occupationally
exposed to asbestos, metal work, paper pulp, or organic dusts. Based on
measurements of the alpha energy concentration at the mines, and a
comparison of smoking habits between underground and surface miners,
the authors concluded that not all of the excess lung cancer for the
underground miners was attributable to radon daughter exposures and/or
smoking. A stronger conclusion may have been possible if the cohort had
been larger.
     Ames et al. (1984). MSHA has taken account of this study,
which made no attempt to evaluate cancer effects, under the heading of
``Chronic Effects other than Cancer.'' The commenter repeated MSHA's
statement (in the proposed risk assessment) that the investigators had
not detected any association of chronic respiratory effects with diesel
exposure, but ignored MSHA's observation that the analysis had failed
to consider baseline differences in lung function or symptom
prevalence. Furthermore, as acknowledged by the investigators, diesel
exposure levels in the study population were low.
     Ames et al. (1983). As discussed later in this risk
assessment, under the heading of ``Mechanisms of Toxicity,'' this study
was among nine (out of 17) that did not find evidence of a relationship
between exposure to respirable coal mine dust and an increased risk of
lung cancer. Unlike the Australian mines studied by Christie et al.
(1995), the coal mines included in this study were not extensively
dieselized, and the investigators did not relate their findings to
diesel exposures.
     Ames et al. (1982). As noted earlier under the heading of
``Acute Health Effects,'' this study, which did not attempt to evaluate
cancer or other chronic health effects, detected no statistically
significant relationship between diesel exposure and pulmonary
function. However, the authors noted that this might have been due to
the low concentrations of diesel emissions involved.
     Armstrong et al. (1979). As discussed later in this risk
assessment, this study was among nine (out of 17) that did not find
evidence of a relationship between exposure to respirable coal mine
dust and an increased risk of lung cancer. As pointed out by the
commenter, comparisons were to a general population. Therefore, they
were subject to a healthy worker effect for which no adjustment was
made. The commenter further stated that ``diesel emissions were not
found to be related to increased health risks.'' However, diesel
emissions were not mentioned in the report, and the investigators did
not attempt to compare lung cancer rates in exposed and unexposed
miners.
     Attfield et al. (1982). MSHA has taken the results of this
study into account, under the heading of ``Chronic Effects other than
Cancer.''
     Attfield (1979). MSHA has taken account of this study,
which did not attempt to evaluate cancer effects, under the heading of
``Chronic Effects other than Cancer.'' Although the results were not
conclusive at a high confidence level, miners occupationally exposed to
diesel exhaust for five or more years exhibited an increase in various
respiratory symptoms, as compared to miners exposed for less than five
years.
     Boffetta et al. (1988). This study is discussed in two
places above, under the headings ``Studies Involving Miners'' and
``Best Available Epidemiologic Evidence.'' The commenter stated that
``the study obviously does not demonstrate risks from dpm exposure.''
If the word ``demonstrate'' is taken to mean ``conclusively prove,''
then MSHA would agree that the study, viewed in isolation, does not do
this. As explained in the earlier discussion, however, MSHA considers
this study to contribute to the weight of evidence that dpm exposure
increases the risk of lung cancer.
     Costello et al. (1974). As discussed later in this risk
assessment, this study was among nine (out of 17) that did not find
evidence of a relationship between exposure to respirable coal mine
dust and an increased risk of lung cancer. Since comparisons were to a
general population, they were subject to a healthy worker effect for
which no adjustment was made. Diesel emissions were not mentioned in
the report.
     Gamble and Jones (1983). MSHA has taken account of this
study, which did not attempt to evaluate cancer effects, under the
heading of ``Chronic Effects other than Cancer.'' The commenter did not
address MSHA's observation that the method of

[[Page 5624]]

statistical analysis used by the investigators may have masked an
association of respiratory symptoms with diesel exposure.
     Glenn et al. (1983). As summarized by the commenter, this
report reviewed NIOSH medical surveillance on miners exposed to dpm and
found that ``* * * neither consistent nor obvious trends implicating
diesel exhaust in the mining atmosphere were revealed.'' The authors
noted that ``results were rather mixed,'' but also noted that ``levels
of diesel exhaust contaminants were generally low,'' and that ``overall
tenure in these diesel equipped mines was fairly short.'' MSHA
acknowledges the commenter's emphasis on the report's 1983 conclusion:
``further research on this subject is needed.'' However, the authors
also pointed out that ``all four of the chronic effects analyses
revealed an excess of cough and phlegm among the diesel exposed group.
In the potash, salt and trona groups, these excesses were
substantial.'' The miners included in the studies summarized by this
report would not have been exposed to Dpm for sufficient time to
exhibit a possible increase in the risk of lung cancer.
     Johnston et al. (1997). This study is discussed in two
places above, under the headings ``Studies Involving Miners'' and
``Best Available Epidemiologic Evidence.'' MSHA disagrees with the
commenter's assertion that ``the study does not support a health risk
from dpm.'' This was not the conclusion drawn by the authors of the
study. As explained in the earlier discussion, this study, one of the
few containing quantitative estimates of cumulative dpm exposures,
provides evidence of increasing lung cancer risk with increasing
exposure.
     Jorgenson and Svensson (1970). MSHA discussed this study,
which did not attempt to evaluate cancer effects, under the heading of
``Chronic Effects other than Cancer.'' Contrary to the commenter's
characterization, the investigators reported higher rates of chronic
productive bronchitis, for both smokers and nonsmokers, among the
underground iron ore miners exposed to diesel exhaust as compared to
surface workers at the same mine.
     Kuempel (1995); Lidell (1973); Miller and Jacobsen (1985).
As discussed later in this risk assessment, under the heading of
``Mechanisms of Toxicity,'' these three studies were among the nine
(out of 17) that did not find evidence of a relationship between
exposure to respirable coal mine dust and an increased risk of lung
cancer. The extent, if any, to which workers involved in these studies
were occupationally exposed to diesel emissions was not documented, and
diesel emissions were not mentioned in any of these reports.
     Morfeld et al. (1997). The commenter's summary of this
study distorted the investigators' conclusions. Contrary to the
commenter's characterization, this is one of eight studies that showed
an increased risk of lung cancer for coal miners, as discussed later in
this risk assessment under the heading of ``Mechanisms of Toxicity.''
For lung cancer, the relative SMR, which adjusts for the healthy worker
effect, was 1.11. (The value of 0.70 cited by the commenter was the
unadjusted SMR.) The authors acknowledged that the relative SMR
obtained by the ``standard analysis'' (i.e., 1.11) was not
statistically significant. However, the main object of the report was
to demonstrate that the ``standard analysis'' is insufficient. The
investigators presented evidence that the 1.11 value was biased
downward by a ``healthy-worker-survivor-effect,'' thereby masking the
actual exposure effects in these workers. They found that ``all the
evidence points to the conclusion that a standard analysis suffers from
a severe underestimate of the exposure effect on overall mortality,
cancer mortality and lung cancer mortality.'' (Morfeld et al., 1997, p.
350)
     Reger (1982). MSHA has taken account of this study, which
made no attempt to evaluate cancer effects, under the heading of
``Chronic Effects other than Cancer.'' As summarized by the commenter,
``diesel-exposed miners were found to have more cough and phlegm, and
lower pulmonary function,'' but the author found that ``the evidence
would not allow for the rejection of the hypothesis of health equality
between exposed and non-exposed miners.'' The commenter failed to note,
however, that miners in the dieselized mines, had worked underground
for less than 5 years on average.
     Rockette (1977). This is one of eight studies, discussed
under ``Mechanisms of Toxicity,'' showing an increased risk of lung
cancer for coal miners. As described by the commenter, the author
reported SMRs of 1.12 for respiratory cancers and 1.40 for stomach
cancer. MSHA agrees with the commenter that ``the study does not
establish a dpm-related health risk,'' but notes that dpm effects were
not under investigation. Diesel emissions were not mentioned in the
report, and, given the study period, the miners involved may not have
been occupationally exposed to diesel exhaust.
     Waxweiler (1972). MSHA's discussion of this study appears
earlier in this risk assessment, under ``Studies Involving Miners.'' As
noted by the commenter, the slight excess in lung cancer, relative to
the general population of New Mexico, was not statistically
significant. The commenter failed to note, however, that no adjustment
was made for a healthy worker effect and that a substantial percentage
of the underground miners were not occupationally exposed to diesel
emissions.
(v) Summation
    Limitations identified in both positive and negative studies
include: lack of sufficient power, inappropriate comparison groups,
exposure misclassification, statistically insignificant results, and
potential confounders. As explained earlier, under ``Evaluation
Criteria,'' weaknesses of the first three of these types can reasonably
be expected, for the most part, to artificially decrease the apparent
strength of any observed association between diesel exposure and
increased risk of lung cancer. Statistical insignificance and potential
confounders may, in the absence of evidence to the contrary, be
regarded as neutral on average. The weaknesses that have been
identified in these studies are not unique to epidemiologic studies
involving lung cancer and diesel exhaust. They are sources of
uncertainty in virtually all epidemiologic research.
    Even when there is a strong possibility that the results of a study
have been affected by confounding variables, it does not follow that
the effect has been to inflate rather than deflate the results or that
the study cannot contribute to the weight of evidence supporting a
putative association. As cogently stated by Stober and Abel (op cit.,
p. 4), ``* * * associations found in epidemiologic studies can always
be, at least in part, attributed to confounding.'' Therefore, an
objection grounded on potential confounding can always be raised
against any epidemiologic study. It is well known that this same
objection was, in the past, raised against epidemiologic studies
linking lung cancer and radon exposure, lung cancer and asbestos dust
exposure, and even lung cancer and tobacco smoking.
    Some commenters have now proposed that virtually every existing
epidemiologic study relating lung cancer to dpm exposure be summarily
discredited because of susceptibility to confounding or other perceived
weaknesses. Given the practical difficulties of designing and executing
an epidemiologic study, this is not so much an objection to any
specific study

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[[pp. 5575-5624]] Diesel Particulate Matter Exposure of Underground Coal Miners

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