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Institute of Medicine (US) Committee on Asbestos: Selected Health Effects. Asbestos: Selected Cancers. Washington (DC): National Academies Press (US); 2006.

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Asbestos: Selected Cancers.

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2Committee’s Approach to Its Charge and Methods Used in Evaluation

GENERAL APPROACH TO EVIDENCE REVIEW

The committee was charged with assessing the evidence concerning the causation of selected cancers, other than lung cancer and mesothelioma, by exposure to asbestos fibers. The charge required that the committee compile and review the available evidence, attempting to identify all relevant epidemiologic studies, and then evaluate whether the evidence was sufficient to infer the existence of a causal relationship. There are now well-established models for meeting the charge, dating as far back as the landmark 1964 report of the US surgeon general on smoking and health (HEW 1964), which reached the conclusion that smoking causes lung cancer and other diseases. That report assembled the full body of relevant scientific evidence and evaluated it according to formal guidelines. Abundant, comprehensive reviews of various other agents have since been conducted to gauge whether the sets of evidence associating them with particular health outcomes warrant causal conclusions.

Established templates for reviewing scientific evidence set out approaches for gathering evidence and assessing its sufficiency to infer causality of association. With regard to obtaining evidence for review, the approach needs to involve clearly specified search criteria that facilitate collection of all potentially relevant studies for evaluation. For some purposes, there may also be an attempt to capture relevant reports in the “gray literature” (non-peer-reviewed or unpublished findings) to obtain the full set of relevant data and to ensure that publication bias does not skew the evidence evaluated, as may occur when datasets are gathered exclusively from peer-reviewed publications. In the case of an as intensively studied agent as asbestos, however, the committee considered that the findings of most studies would be published. It is possible that only statistically significant or particularly notable results on nonrespiratory endpoints would be included in the published reports on the cohort studies, and this could lead to reporting bias for cancers at the designated sites.

Once germane studies have been identified, they may undergo evaluation so that they can be classified according to the quality of the evidence that they provide. They may be evaluated systematically according to a standardized protocol and placed into tiers on the basis of their quality. In a systematic review, results of studies may be qualitatively evaluated and subjected to an overall judgment; additionally, data may be combined to derive a quantitative summary and to explore variation in results among studies. Analyzing aggregated summaries of studies is often referred to as meta-analysis; on occasion, data from studies are obtained at the level of individual participants and jointly analyzed, an approach sometimes referred to as pooled analysis. Statistical approaches for quantitative meta-analysis have been developed (Petitti 2000), as well as methods for detecting publication bias in meta-analyses (Peters et al. 2006).

Guidelines for causal inference have long been used; perhaps the best-known are those offered in the first report of the US surgeon general on smoking and health (HEW 1964):

  • The consistency of the association.
  • The strength of the association.
  • The specificity of the association.
  • The temporal relationship of the association.
  • The coherence of the association.

The guidelines provide principles for interpreting epidemiologic evidence in a context set by biologic plausibility and the coherence of different lines of evidence. This committee has used such criteria in meeting its charge.

Specificity refers to a unique exposure-disease relationship, which is characteristic of diseases caused by infectious organisms. The concept has also been applied for investigating the contribution of physical and chemical agents to disease (Weiss 2002). The association of asbestos with mesothelioma constitutes one of the few examples of a high degree of specificity for a toxic agent and cancer risk, but the committee gave minimal weight to the criterion of specificity because the cancer sites under consideration have multiple causes and more will likely be identified.

From the outset, the committee recognized that asbestos fibers are known to be carcinogenic and that its conclusions with regard to the cancers specified in its charge would rest heavily on the epidemiologic evi dence. The committee also believed that information on fiber dose to the target organs would be relevant, because the risk of cancer associated with asbestos fibers is known to be dose-dependent. The committee also gathered information on mechanisms by which asbestos fibers are carcinogenic.

That broad array of evidence was reviewed and synthesized by the committee to make its final determination as to the strength of evidence in support of an inference of causality. A variety of descriptors have been used by committees of the Institute of Medicine (IOM), the National Research Council, and other entities in characterizing the strength of evidence (see NRC 2004 for a review). The classification schemes generally include a category for circumstances in which the data are inadequate for making a judgment and a category for evidence of no association. Most schemes include several categories of evidence indicative of a possible causal association ranging from uncertain to fully certain; two or three categories generally serve for this purpose. The IOM approach has also distinguished between association and causality.

For this report, the committee selected a classification scheme similar to that used in the 2004 report of the US surgeon general on smoking and health (HHS 2004). That report used two categories in reference to evidence in support of a causal determination: sufficient and suggestive. Because the legislation mandating this committee’s review requested only a determination of whether asbestos played a causal role in inducing these additional types of cancer, it was the committee’s judgment that insertion of an additional category for evidence more weakly supportive of causation would unnecessarily generate another, most probably arbitrary distinction in classifying the evidence below the threshold for causal inference. Therefore, the committee adopted the four-category scheme of the recent US surgeon general’s report on smoking and health (HHS 2004) as adequate to meet its charge:

  • Evidence sufficient to infer a causal relationship.
  • Evidence suggestive but not sufficient to infer a causal relationship.
  • Evidence inadequate to infer the presence or absence of a causal relationship, which encompasses evidence that is sparse, of poor quality, or conflicting.
  • Evidence suggestive of no causal relationship.

For the purpose of addressing the charge and the designation of “cause,” the committee required that the evidence be judged sufficient. The category of suggestive “but not sufficient” potentially comprises a range of evidence and uncertainty that does not rise to the level of certainty needed for the designation of causality.

For the cancer sites specified in its charge, the committee also needed to consider how asbestos fibers could jointly act with other causal agents to affect risk. For cancers of the larynx and esophagus, tobacco and alcohol are well-established carcinogens, and most cases are attributable to their independent and joint actions. Smoking is also a cause of stomach cancer. Various risk factors for cancers of the colon and rectum are under investigation, including diet and physical activity.

Epidemiologists use the terms effect modification and interaction in referring to the joint consequences of several agents in causing disease. Effect modification in a positive direction, called synergism, increases risk in those exposed to two or more risk factors beyond expectation based on their independent effects. Negative effect modification is called antagonism. To assess the presence of effect modification, stratified and multivariate analytic approaches can be used. The presence of synergism implies that those exposed to one risk factor are at heightened risk when exposed to the additional, interacting factors.

Effect modification by tobacco-smoking has been considered in studies of the association between asbestos exposure and lung cancer. For investigating such effect modification, information is needed on both asbestos exposure and smoking; this requirement is met by some studies, most often of a case-control design. A recent evaluation of the evidence concerning effect modification by smoking on the risk of lung cancer associated with asbestos exposure by the International Agency for Research on Cancer (IARC 2004) concluded that there is synergism; the pattern has not been precisely characterized, however, in part because of methodologic issues.

A related issue is whether asbestos fibers alone can cause cancers at the designated sites. Epidemiologists have conceptually classified causal agents as necessary (presence is required), sufficient (presence is not required, but the agent can cause the disease by itself), and neither necessary nor sufficient (Goodman and Samet 2006, Rothman and Greenland 1998). That classification has proved useful in classifying the span of causation from diseases linked to specific agents to diseases with multiple causes, such as coronary heart disease. For example, causal microbial agents are necessary for infectious diseases and tobacco-smoking alone appears sufficient for lung cancer although there may be genetic and other nontoxicologic factors that lead one smoker but not another to develop lung cancer. Similarly, asbestos fibers are considered sufficient for mesothelioma. Goodman and Samet (2006) stress that for multifactorial diseases, such as cancer, most risk factors are to be regarded as being in the neither-necessary-nor-sufficient category. Agents that behave as synergens, amplifying the effect of another carcinogen, whether or not they appear to function as carcinogens by themselves, would be regarded as causal factors. Ultimately, a convincing demonstration that the presence compared with absence of asbestos exposure, all else being equal, would increase the population risk of cancer at one of the sites under review would establish a causal role for asbestos for that type of cancer.

Finally, although it considered the precision of measures of association reported by the researchers when interpreting the weight of evidence provided by various epidemiologic studies, the committee does not regard statistical significance as a rigid basis for determining causality. A full evaluation needs to consider all types of relevant evidence and take into account uncertainties beyond those of a solely statistical nature.

EVIDENCE CONSIDERED

Assembly of Literature Database

The biomedical literature concerning asbestos is vast (about 25,000 citations in the searchable reference databases MEDLINE and EMBASE), but much of it exclusively addresses asbestos’s role in causing asbestosis, lung cancer, and mesothelioma. Given the committee’s circumscribed task of answering the question of whether this known carcinogen plays a causal role in producing pharyngeal, laryngeal, esophageal, stomach, or colorectal cancer (“selected cancers”), the committee saw no need to revisit the entire body of information on asbestos’s biologic activity or even to review the entire epidemiologic literature on asbestos exhaustively. The subset of epidemiologic literature referring to the selected cancer sites, however, did need to be identified comprehensively, retrieved when possibly pertinent to the task, and thoroughly reviewed when found to be relevant.

MEDLINE and EMBASE are biomedical databases of bibliographic citations and abstracts drawn from biomedical journals (more than 4,600 and 6,500, respectively) published in over 70 countries. Their broad international coverage can be regarded as exhaustive for the developed countries. To ensure the necessary completeness of the desired subset of asbestos literature, those databases were searched by using detailed expansions of synonyms and CAS numbers for asbestos in combination with global search terms for the selected cancers. Before secondary documents and repeated publication of the same material in an English journal and a non-English native language publication were culled, these searches retrieved about 450 English citations and about 100 foreign-language citations.

The secondary literature (e.g., ATSDR 2001; Becklake 1979; EPA 1986; IARC 1977, 1987; Kleinfeld 1973; Landrigan et al. 1999; Li et al. 2004; OSHA 1986) was used to identify articles about the cohorts that have served as the basis of conclusions concerning asbestos’s involvement in asbestosis, mesothelioma, and lung cancer. In addition, the reference lists of previous reviews and meta-analyses of asbestos’s possible role in the etiology of the “selected cancers” were also searched to identify the primary citations considered. Although the committee would not necessarily accept every study given weight in earlier assessments, the members wanted to be aware of all literature that had been considered. Site-specific reviews were screened for citations on digestive system cancers (Hallenbeck and Hesse 1977, Schneiderman 1974), gastrointestinal cancers (Edelman 1988, Frumkin and Berlin 1988, Goldsmith 1982, Goodman et al. 1999, Kanarek 1989, Miller 1978, Morgan et al. 1985), stomach cancer (Smith 1973), colorectal cancer (Homa et al. 1994, Weiss 1995), colon cancer (Gamble 1994), and laryngeal cancer (Browne and Gee 2000; Chan and Gee 1988; Edelman 1989; Goodman et al. 1999; Griffiths and Molony 2003; Guidotti et al. 1975; Kraus et al. 1995; Libshitz et al. 1974; Liddell 1990; Parnes 1996, 1998; Smith et al. 1990). The primary publications identified in this manner consisted largely of site-specific case-control studies.

“Asbestos cohorts” were defined as those having asbestos as a major exposure and as a primary research focus. That excluded studies of cohorts for which asbestos was merely a component of a poorly characterized, complex exposure; was a confounder of the exposure of real interest to the researchers; or was mentioned as a hypothesized explanation of an observed excess risk. We sought to gather a comprehensive set of citations concerning the asbestos cohorts, but to limit procurement of hard copies to articles most relevant to our mission—the most recent or comprehensive publications on a given cohort and articles specifically addressing the five selected cancers, asbestos exposure, or distribution of asbestos fibers to tissues. All citations related to a given study population were grouped on a spreadsheet to characterize the cohort and how it had been researched over the years. For the cohorts that ultimately provided information on the selected cancers, information from this spreadsheet is tabled in Appendix B. That procedure facilitated recognition of whether any additional publications pertained to a pre-existing study cohort and thereby avoided double-counting of evidence. It also aided in identification of which articles should be obtained as hard copies.

Other search operations were performed manually in PubMed to augment the citations downloaded from MEDLINE and EMBASE into ProCite (2003). PubMed, which contains all MEDLINE citations and an additional 5%, mostly from less prominent foreign journals, is readily accessible for on-line queries and for recovery of citations for importation into ProCite.

To capture any other publications related to the cohorts that might contain information about the “selected cancers” (which might have been deemed peripheral to demonstrating the “known health outcomes”), the names of researchers identified in their author lists were manually searched in PubMed for other asbestos-related publications. Special attention was paid to seeking updates of the identified cohorts that superseded those considered for the evaluations of lung cancer and mesothelioma.

Unless it is found to be associated with the cancer in question, an occupational exposure addressed in a case-control study often is not mentioned in the title, abstract, or keyword field scanned during database searches. Therefore, to avoid bias toward positive results and to ensure full retrieval of case-control studies that considered asbestos and that were published through August 2005, PubMed was screened for cancer, occupation, and case-control (and variants) in combination with synonyms for the selected cancer sites without stipulation of an asbestos-related keyword.

The final ProCite database contains about 2,500 citations. For some-what more than a fourth of them (754), hard copies were obtained and more closely evaluated for pertinence. Ultimately, about 300 publications directly contributed evidence to our evaluation. Results were abstracted from 36 citations on case-control studies and from about 80 citations on the 40 informative cohort populations for the meta-analyses conducted on epidemiologic findings. Nearly 200 citations contributed asbestos-specific information from animal and in vitro studies, exposure investigations, and mineralogic characterizations.

Selection of Studies for Inclusion

The citations identified by the search procedure described in the previous section were screened for further consideration on the basis of their abstracts. Copies of reviews, meta-analyses, and other secondary sources were obtained for use in searching as described above and for background information, but the cancer-site-specific content was not considered by the committee members before they conducted their own evaluation. For its evidentiary database, however, the committee was interested only in reports of primary investigations. A comprehensive dataset on all asbestos’s potential health effects was not being sought, but a wide net was cast by retrieving copies of reports involving the selected cancer sites that might address asbestos exposure specifically and of asbestos-exposed cohorts that might present information on the selected sites of this review along with data on the health outcomes that are now accepted to be asbestos related.

The committee limited the epidemiologic results in its evidentiary database to findings of appropriately designed cohort and case-control studies. Cross-sectional studies, ecologic studies, and case series could at most provide supportive evidence. Furthermore, the committee decided that studies of asbestos in drinking water, primarily ecologic in design, did not provide information that was directly pertinent to the charge.

Although the committee wanted to be as comprehensive as possible, constraints of time and accessibility prevented securing original articles for a large portion of the foreign-language citations and arranging for their translation. When English abstracts were available, they usually stated ma jor findings and conclusions, but the committee’s consensus was that study methods needed to be addressed in detail if the reliability of a citation’s results were to be evaluated. Therefore, all foreign-language articles were set aside. Consideration of available abstracts and tables did not suggest that the findings reported in those documents differed systematically from findings reported in their English-language counterparts.

Articles that were eligible for inclusion in the evidentiary database were evaluated from several perspectives, as set forth below to determine the overall quality of studies and the consequent reliability of estimates of relative risk (RR) derived from them. As discussed in more detail in the following sections, the design of each study was assessed in terms of how the study sample (cohort members or cases) and comparison group were selected, how the health outcome was determined, how exposure was characterized, and how adequately possible biases and confounders had been addressed. For some of the committee’s analyses, subgroups of studies were selected on the basis of design characteristics.

CRITERIA FOR EVIDENCE EVALUATION

Fiber Type

The committee recognized that there is evidence suggesting that the risk associated with asbestos exposure for development of mesothelioma (and possibly of lung cancer) may vary by fiber type. Controversy continues (for example, Hessel et al. 2004, Rice and Heineman 2003) as to whether there is an absolute difference in the toxicity of amphibole and serpentine (chrysotile only) forms of asbestos and whether only amphibole fibers have carcinogenic potential, particularly for mesothelioma, the neoplasm for which a difference seems most apparent. Recent reviews suggest that rather than having no carcinogenic activity, chrysotile has a generally lesser degree of potency than amphibole fibers, and that the various types of amphibole fibera differ in the extent of their biological activity (Britton 2002, IPCS 1998, Roggli 2006, Roggli et al. 1997, Suzuki et al. 2005). In its initial assessment of its charge, the committee evaluated whether its report could address whether associations of asbestos exposure with risk for the designated cancers either depended on the presence of specific type of fibers or varied with type of fiber. With the sole exception of the Montreal study (Dumas et al. 2000; Parent et al. 1998, 2000), the case-control studies did not provide information on fiber type, as self-reported work histories were generally the basis for exposure estimation and the resulting exposure estimates were not specific to fiber type. Consequently, the potentially relevant evidence on fiber type came almost exclusively from the cohort studies of asbestos-exposed populations, and specifically from those that have had relatively pure exposures to a specific fiber type, such as the crocidolite mining and milling workers in Western Australia. In considering the body of evidence from cohort studies for the designated cancer sites, the committee found only limited literature that was specific as to fiber type. The committee considered the physical and chemical characteristics that distinguish the major fiber types and the potential relevance of these characteristics to relative carcinogenicity of the fiber types. The implications of these physical and chemical differences among fiber types for human carcinogenesis have not been extensively studied, specifically under circumstances of occupational exposure. Current evaluations favor the hypothesis that carcinogenicity is not limited to asbestos fibers of the amphibole type (Britton 2002, IPCS 1998, Roggli 2006, Roggli et al. 1997, Suzuki et al. 2005). Consequently, the committee’s report describes the level of causal inference in relation to asbestos, without specifying the type.

Grouping of Evidence by Cancer Site

The cancers that this committee was asked to consider are a diverse group of tumors that develop from the upper portions of the respiratory and digestive tracts to the colon and rectum. Even cancers that occur in tissues contiguous to the mouth and pharynx, and that are conventionally grouped together as “head and neck” cancers, differ markedly in their risk factors and descriptive epidemiology. In many epidemiologic studies that have examined the association of asbestos with the cancers of interest in this report, sites have been grouped into various categories to allow statistical analyses of rather sparse data, even when cancers at the subsites have very different etiologies. Optimally, one would consider the evidence concerning these cancers in groupings that reflect generally similar etiology, but extracting what information is available from epidemiologic studies conducted over the last half century under circumstances of evolving understanding of biologic mechanisms and epidemiologic analysis make this objective unattainable.

Given the committee’s intention of considering the available data in a comprehensive and inclusive fashion, however, results were first abstracted with notations as to exactly which anatomic sites the researchers were reporting on, according to specific International Classification of Disease (ICD) codes for causes of death (ICD-9; although now superseded, version 9 was in effect at the time of most of the deaths recorded in the studies reviewed) or the comparable oncology codes for cancer type (ICD-O-3). Table 2.1 indicates the equivalence between those coding systems for the cancers under consideration, with some of the common phrases used by researchers to report findings on grouped sets of sites, which often are not accompanied by precise designations.

TABLE 2.1. Standard Codes and Nonstandard Groupings Used to Characterize “Accepted” and “Selected” Cancers.

TABLE 2.1

Standard Codes and Nonstandard Groupings Used to Characterize “Accepted” and “Selected” Cancers.

The committee did attempt to note whether effects might be associated with more specific classifications that would be more meaningful from an etiologic perspective. The committee also noted that ICD codes do not capture changes in the subsites involved or their histopathologic classification, which was of particular relevance for esophageal and stomach cancers. When the available data were assembled, the committee considered groupings no broader than “pharynx with oral or buccal cavity,” “larynx with epilarynx” (larynx plus portions of the oropharynx specified as ICD codes 146.4, 146.5, and 148.2), and “rectum with colon or intestines” to be meaningful.

Because of the committee’s requirement for relatively specific groupings of sites, a considerable number of cohorts were judged uninformative for the “selected cancers.” Those cohorts may have been studied intensively with repeated follow-up of vital status, but in most cases the researchers’ primary interest was respiratory disease, both malignant and nonmalignant, and information on the cancers of concern in this review was not reported or analyzed.

Study Designs

Epidemiologic designs applied in investigations of environmental and occupational risk factors for cancer are primarily of three types: cohort studies of defined groups (such as worker populations), case-control studies, and “ecologic” studies that compare rates in geographic regions defined by exposure characteristics. Epidemiologic studies can also be classified as exposure-based or general-population-based depending on whether the source population is defined as an exposed group (such as workers in a particular industry or residents of a contaminated community) or the population at large.

Occupational and Environmental Cohort Studies

In general, exposure-based cohort and nested case-control studies (in which cases and controls are selected from a well-defined cohort) provide the most direct observational evidence of associations with occupational carcinogens and industry-related chemicals that may reach the general environment. Their primary advantage is the possibility of linking clearly specified exposures to health outcomes. Limitations of most exposure-based studies are the low frequency of some health outcomes (such as site-specific cancers) and the absence or sparseness of data on lifestyle or constitutional disease risk factors (such as tobacco-smoking and diet) that may confound observed associations with risk.

Population-Based Case-Control Studies

In contrast, population-based case-control studies have the distinct advantages, compared with exposure-based studies, of accruing relatively large case groups and providing an opportunity to obtain data on important potential confounding factors. The weakest aspect of most population-based case-control studies is the poor quality of the exposure characterization, which often lacks agent specificity or quantification.

Ecologic Studies

Although ecologic studies may yield etiologic clues, causal inference is constrained because exposures and health outcomes are correlated at an aggregate level (geographic or population) rather than for individual study subjects. They tend to be most suitable for suggesting exposure-disease relations that may lead to more-focused cohort or case-control studies. Consequently, ecologic studies were not included in the database of epidemiologic studies evaluated and integrated by this committee.

The committee does not view either the case-control or cohort design as being intrinsically preferable or stronger than the other, and does not believe one type should be weighted more heavily than the other. Consideration of the results from both types of design permits viewing the real-world outcomes available for observation by epidemiologists from two different perspectives, with studies of samples defined on the basis of exposure (cohort studies) and with studies of samples defined on the basis of health outcome (case-control studies). Having information from both these types of studies, along with the incorporation of findings from controlled experimentation (as discussed in the coherence criterion section of the causal integration for each cancer site), helps to ensure that the vulnerabilities of one type of evidence are countered by the strengths of the other.

Measurement of Exposure and Outcome

Exposure

The accuracy of exposure assessment is a major determinant of the informativeness of a study for causal inference and of the validity and reliability of risk estimates that can be drawn from study data. Inaccurate exposure assignment can bias study findings with the consequences depending on whether it is nondifferential or differential. Generally, although not always, nondifferential or random exposure misclassification will diminish the likelihood of detecting a true association between an exposure and disease. For asbestos, exposure intensity, timing, and duration are the most relevant considerations for exposure assessment. Sources of exposure misclassification include missing or incomplete data on concentrations or work time, erroneous measurements, and poor sources of data (such as statement of usual occupation on death certificates), but the use of crude exposure classifications (such as “ever exposed” vs “never exposed”) is often necessitated by the lack of documentation on actual exposure. Self-reporting of exposure in response to lists of agents can also be a source of misclassification in population-based case-control studies. Because exposures that occurred far in the past are relevant to cancer, the absence of quantitative data and even the lack of a basis for assigning qualitative exposure rankings are common limitations in assessing exposures.

The method used to estimate the exposures of study subjects is crucial in determining the quality of case-control studies. In contrast with cohort studies, it is not feasible to assess asbestos exposure quantitatively in case-control studies using actual measurement data. The most useful case-control studies are those that assign a magnitude or probability of exposure (on an ordinal basis) by using a lifetime work history with details of work activities. That technique was pioneered by researchers in Montreal who used it in several publications included in this review (Dumas et al. 2000; Goldberg et al. 2001; Parent et al. 1998, 2000). In some studies, levels of exposure have been assigned on the basis of occupation or industry using a job-exposure matrix (JEM), occasionally even taking the era when exposure occurred into consideration. Studies that assess exposure with direct questions (for example, “Were you ever exposed to asbestos?”) are prone to recall bias and may also suffer from widely varied interpretations among participants of what constitutes exposure. Nonetheless, data derived in such a crude fashion may still yield useful information.

This committee’s review did not include hypothesis-generating studies that assessed cancer risks only in association with a large number of occupations or industries and then interpreted the results a posteriori on the basis of exposures assumed to occur in the jobs or industrial sectors found to have increased risks. Some studies used the “usual” occupations and industries entered on death certificates as a source of exposure information, but the committee did not consider them to be adequately reliable for inclusion in this review (Andrews and Savitz 1999; Selikoff 1992), even when interpreted with a JEM. Death certificates may be completed by medical personnel who know little about the work histories of the deceased, they list only a single job, and they do not include dates of employment. Although useful for surveillance, death certificates are a crude source of data for etiologic investigations, particularly for manufacturing workers who may have held many jobs.

The metrics of exposure derived across studies were so diverse that a hierarchy by potential quality could not be applied. The committee adopted a pragmatic approach in order to assess whether classifying a given study population along even a crude exposure gradient would yield evidence for a dose-response relationship between asbestos exposure and risk. The committee recognized limitations of the data available for this purpose and was not seeking accurate quantitative estimates. Initially, the committee defined three levels of exposure-assessment method (EAM) quality for each of the two design types and graded the informative studies accordingly. In practice, it turned out for both designs that the two higher quality grades (now subsumed in EAM = 1) corresponded to the capability to do analyses on dose-gradients (although for the selected cancer sites, the needed data were not necessarily presented in the articles). The committee did consider that evidence of a dose-response relationship is a strong supporting element for inferring causality. Given the limitations of the data available, failure to find an indication of a dose-response relationship was not viewed as evidence against a causal relationship.

Outcome

The primary outcomes for cancer etiology studies are typically cancer mortality and cancer incidence (diagnosis). Cancer mortality is usually ascertained from the underlying cause of death indicated on a death certificate. The National Death Index is an electronic nationwide resource for specific causes of death in the United States; some other countries maintain similar data. The validity of a recording of cancer on a death certificate has been examined and found to be fairly reliable for epidemiologic studies for rapidly fatal cancers (such as lung cancer) (D’Amico et al. 1999, Percy et al. 1981, Sathiakumar et al. 1998). Cancers that metastasize, however, may be listed incorrectly on death certificates, and diagnosed cancers that do not result in death may be missed (as is likely to be the case for laryngeal cancer for which the survival rate is relatively high). Selikoff and Seidman (1992) found death certificate information on primary and contributing causes of death to be problematic for asbestos-related diseases in general, while investigations tracking patients known to have oral and oropharyngeal cancers (Leitner et al. 2001) or colorectal cancers (Ederer et al. 1999) found death certificate information did not reflect the earlier diagnosis with any certainty. In addition, information on death certificates often lacks specificity regarding primary site or histology (for example, simply “pharynx,” rather than “oropharynx”). There is no reason to expect the frequency of such errors to be linked to asbestos exposure, but they do decrease the sensitivity of results to any real effect.

Cancer incidence is typically ascertained from a cancer registry— corporation-, state-, or county-based in the United States or national in some countries. The validity of a cancer diagnosis from a statewide cancer registry is generally high because state registries require medical-record validation.

The cohort studies considered by the committee were carried out in multiple locations, and their findings were reported from the 1950s on. In most of the studies, cause-specific mortality was the principal outcome measure. Mortality is a useful indicator of disease occurrence (incidence) for diseases with poor survival, such as lung cancer. The validity of mortality as an indicator of cancer incidence also depends on the accuracy of both identification of cause of death and its coding. Undoubtedly, there was some degree of misclassification in the assignment of cause of death in the cohort studies considered. If random, the result would have been a reduction in sensitivity to detect an effect. As clinicians became aware of the associations of asbestos with various diseases, there may have been a bias toward diagnosing diseases such as lung cancer at higher rates among workers in known asbestos-related industries than in the population at large.

All the case-control studies considered in this review reported results in terms of cancer incidence rather than mortality and identified cases from hospital listings or regional government tumor registries, which are population-based. Aside from nested case-control investigations conducted in the asbestos cohorts under consideration, the committee did not consider nested case-control studies of occupational cohorts that did not have asbestos as a major exposure. Case status may have been determined histologically or from death certificate information, but studies that used histologic confirmation were accorded greater weight in the selection process. In most studies, randomly selected population controls were used. In the studies published by Siemiatycki’s group in Montreal (Dumas et al. 2000; Goldberg et al. 2001; Parent et al. 1998, 2000), the controls consisted of a mix of population controls and other controls with other types of cancer.

Validity

Thorough and valid ascertainment of exposures and health outcomes is critical if epidemiologic research is to be informative. Validity is determined by the extent to which the investigators can minimize bias that may result from improper selection of index or comparison groups (exposed and non-exposed subjects in a cohort study, cases and controls in a case-control study), misclassification of health outcome or exposure variables, or failure to minimize confounding by disease risk factors that are also related to the exposure under study.

Precision

Precision of exposure estimates reflects the magnitude of measurement error due to the analytic sampling instrument or the number of measurements made (such as air samples of asbestos fibers). Studies with more subjects tend to be more informative than smaller studies, provided that study size is not achieved at the cost of reduced reliability and validity of the exposure-assessment approach. Sample size is reflected in the precision of estimates of effect as measured by the width of the confidence interval (CI) of an observed RR. Although large studies are desirable, relatively small studies with a high degree of validity are preferable to large studies with questionable validity.

Bias

Detailed discussions of consequences and methods to reduce the three forms of bias—confounding, selection, and information—are provided in standard epidemiologic texts (Rothman and Greenland 1998). The healthy-worker effect (and the related healthy-worker survivor effect) is a source of bias that is both peculiar to occupational epidemiology and ubiquitous, so it warrants further elaboration. As described below, the healthy-worker effect can include elements of both confounding bias and selection bias.

Confounding Bias

Many occupational cohort studies compare disease rates between a worker cohort and the general population. Although comparisons of this type give some indication of overall patterns of relative disease occurrence in the worker cohort, they may also be affected by confounding bias. Specifically, workers in a particular trade may differ from the general population in lifestyle characteristics and health status. For example, tobacco-smoking and alcohol-consumption patterns, known risk factors for laryngeal cancer, may be quite different between blue-collar industrial workers who are exposed to asbestos and the general population, which includes people from all socioeconomic classes. Contrasts in laryngeal-cancer incidence between a worker cohort and the general population might thus be confounded if smoking is not taken into account. The committee could only gauge the potential for confounding to have increased risk estimates from the case-control studies. For comparisons within a specific worker cohort, confounding by smoking and alcohol may be less problematic than in studies in more diverse populations (Kriebel et al. 2004).

Health status also commonly differs between worker and general-population groups because healthy people are selectively hired into the workforce and the general population includes people who are too sick to work; workers may also benefit from the health advantages of higher incomes and employee health plans. Differential employment rates by health status leads to what is known as the healthy-worker effect; it often results in mortality risk estimates that spuriously suggest a health-protective effect in association with occupational exposures. The healthier workers also tend to stay employed longer, resulting in a confounding bias when workers with low cumulative exposure are compared with more highly exposed workers. Thus, the healthy-worker survivor effect may cause bias even in a study based on internal comparisons.

The case-control studies considered by the committee varied a great deal with respect to control for confounding. Nearly all controlled for age and sex either by virtue of original matching criteria for control selection, by statistical adjustment, or by simply reporting on men and women separately. They vary, however, in whether they controlled for smoking, alcohol use, birthplace, region, diet, obesity, physical activity, and educational status. Studies that controlled for smoking and alcohol were given greater weight for pharyngeal and laryngeal cancers.

Selection Bias

The healthy-worker effect and the healthy-worker survivor effect can be viewed as a result of selective hiring of healthy people or of keeping less healthy workers away from exposure in the workplace. The healthy-worker survivor effect is most pronounced for cardiovascular and obstructive lung diseases, but it may also bias research findings for various cancers. Case-control studies are subject to selection bias if controls are poorly chosen in a manner related to the probability of exposure.

Information Bias (Misclassification of Exposure or Outcome)

It is possible for differential misclassification, a classification error associated with the value of other variables, to result in bias toward either overestimation or underestimation of an effect. For instance, the tendency of people who have a disease to search for explanations of their condition may make them more likely to report an exposure of interest, so the possibility of recall bias needs to be anticipated in case-control studies. Independent assessments of documented work histories by occupational hygienists are often applied in an effort to remedy some of the error associated with self-reported exposures in population-based case-control studies. The problem also provides a motivation for using hospital- or registry-identified controls.

In most circumstances, nondifferential misclassification of exposure or health outcome will obscure detection of a real effect by producing an estimated risk closer to the null (RR = 1.0). Of necessity, epidemiologic studies incorporate surrogate exposure indicators for the relevant biologic dose. Exposure and dosimetric modeling may be applied to estimate this dose more precisely, but improper modeling assumptions may introduce misclassification. Similarly, the lower sensitivity of cancer-mortality studies, than of cancer-incidence studies, for cancers with high survival could be regarded as the result of misclassifying deceased people if cancer incidence is the investigation’s objective, because the presence of an earlier, nonfatal cancer is unlikely to be recognized.

Statistical Analysis

The validity of a study requires application of appropriate methods for statistical analysis of the data.

Precision

The size of the study population will contribute directly to the precision with which the target effect is estimated; precision is reflected in the standard error or CI associated with the estimated effect. For cohort studies, precision of the estimated effects (and therefore power to test hypotheses) is driven primarily by the expected number of events, which is a function of person-years of follow-up and incidence. For example, two studies with equal numbers of person-years of follow-up will have estimated effects with different precision if one deals with a more common cancer than the other. For case-control studies, precision of estimated effects depends primarily on the size of the sample of cases and controls but also can be affected by adjustment for confounders or method of sampling (matched vs unmatched pairs). Precision thus depends on sample size but may be affected by other characteristics of a study design or method of analysis.

Statistical Modeling

RRs adjusted for confounding can be derived by stratification, by matching on confounders, or by including potential confounders in multiple regression models in which the exposure of interest is the primary independent variable. Models are sometimes preferred over stratified contingency tables because data become sparse in stratified analyses when multiple confounders are present. The most common risk models in environmental and occupational epidemiology are logistic regression, Poisson regression, and Cox proportional hazards models. Parameters estimated from these models can be conveniently interpreted as adjusted odds ratios, mortality or incidence-rate ratios, and hazard-rate ratios, respectively. It is important to keep in mind that all the advantages of modeling can be undermined if the underlying assumptions about the distribution of the outcome or form of the exposure-response relationship are mis-specified. These assumptions are generally known to epidemiologists and biostatisticians working in the field, but are rarely laid out and examined in published papers.

Summary

Ultimately, judgments about the role of any environmental agent in the causation of disease must be based on the critical evaluation of observational studies of exposed subjects. Unlike subjects in clinical trials, epidemiologic studies of environmental or occupational causes of disease cannot randomize subjects into exposed and unexposed groups. Thus, results of even the best observational study may be biased. Recognizing that limitation, the challenge is to assess the collective weight of the evidence across multiple studies of each disease endpoint, with particular attention to the validity of exposure ascertainment.

METHODS USED FOR QUANTITATIVE META-ANALYSIS

The units of input for the meta-analysis on each selected cancer site were the most complete risk estimates available on discrete study populations. A single citation could therefore generate more than one datum (such as separate results for men and for women), whereas only the most recent follow-up giving information on one of the selected cancer sites was used from among a series of publications on the same occupational cohort.

For each cancer site, plots were generated depicting all contributing risk estimates with their respective 95% CIs, plus a summary estimated RR with its associated 95% CI. For each cancer site, plots were constructed separately by study type (case-control vs cohort). The summaries were designed to capture an overall characterization of any exposure vs no exposure, and to capture the available evidence of a dose-related effect by summarizing the available information on the effect for the most extreme exposure category vs no exposure.

The committee carefully considered whether to quantitatively summarize the findings from the diverse body of cohort and case-control studies. The studies were carried out in various worker and general-population samples, and their methods differ to varying extents. In this circumstance, the heterogeneity of the evidence can be statistically considered, as was done by the committee in its aggregating approach. The confidence intervals, however, do not fully reflect the range of uncertainty around the pooled estimates, as differences in exposure and outcome ascertainment and different patterns of potential confounding are not taken into account. The plots provide a graphic display of the range of estimates from the cohort and case-control studies.

Given the heterogeneity of the observational evidence considered, the committee gave weight to the consistency of the findings and to the degree of increase in estimated risk, along with whether there was an indication of a dose-response relationship. The committee proceeded despite concerns that the summary estimates generated by its meta-analyses might convey an unfounded degree of precision or certainty. The committee did not consider indicators of statistical significance arising from the meta-analyses as critical determinants in its decision-making. The summary estimates were useful in considering the extent to which methodologic explanations offered an alternative to causation for observed associations.

The first set of plots for each study type summarizes the distribution of estimated RRs associated with any exposure to asbestos (vs none). A second set of plots presents available evidence of a dose-response relationship. In both the case-control and cohort studies, a subset of studies reported RRs across a gradient of exposure; these were used to summarize the effects of “high” exposure to asbestos. Because the definition of high exposure differed by study, we knowingly summarized RRs over an array of definitions.

For case-control studies, we also summarized the distribution of RRs stratified by exposure-assessment method (EAM). For laryngeal and pharyngeal cancers, we stratified the summaries by whether the reported RRs were adjusted for smoking and alcohol use; similar stratification by confounder adjustment was not possible for cancers at other sites because of small numbers of studies in potential strata.

Summary RRs and associated 95% CIs were computed for the set of RRs overall and for each subgroup by EAMs or with and without con founding adjustment. For cohort studies, this was accomplished by using Poisson regression; for case-control studies, the method of DerSimonian and Laird (1986) was applied. Details of how these aggregate estimates were calculated are provided below.

Summary Plots for Cohort Studies

Organization of Summary Plots

Two plots were constructed for each cancer site. The first summarizes the effect of any exposure to asbestos (vs none), and the second summarizes the effect of high exposure vs none. Each summary plot includes the RR and 95% CI for each cohort listed, and a summary RR with an associated 95% CI. The template for summaries of cohort studies of cancer at each site is given in Table 2.2.

TABLE 2.2. Organization of Summary Plots Used for Cohort Studies Informative for Cancer at Each Site.

TABLE 2.2

Organization of Summary Plots Used for Cohort Studies Informative for Cancer at Each Site.

Most of the cohort studies reported results for cancer mortality, but some also, or only, reported on cancer incidence. Incidence is a more comprehensive statistic because it considers all people in whom cancer was diagnosed, not just those who ultimately died from it. Therefore, when there was a choice, incidence findings were reported. A study’s caption on a plot indicates when a standardized incidence ratio was reported rather than a standardized mortality ratio.

Plot 1 includes every cohort with a reported finding for any exposure vs none without reference to study characteristics (such as exposure quality and confounder adjustment). The committee decided that the reliability of an estimate of risk for a given cancer type from simply being in an occupational cohort in comparison with a standard population (that is, being categorized as having had “any exposure”) would not be affected by a study’s thoroughness in determining exposure gradients. Therefore, unlike what was done for case-control results, the cohort results for “any exposure” were not stratified on how exposure quality was measured in the overall study (in which detailed exposure characterization was most often derived for application to respiratory health outcomes). Most cohort studies did not report explicit confounder adjustment, so stratification on this characteristic was not part of the analysis.

Plot 2 presents RRs for the most extreme category of an exposure gradient vs no exposure. We endeavored to capture the estimated effect in the highest reported categories of exposure (vs none) as a means of detecting dose-response relationships; a positive shift of the summary RR on plot 2 relative to plot 1 is viewed as an indicator of a dose-response relationship. One difficulty in capturing a qualitative sense of that phenomenon is the considerable heterogeneity in how “high exposure” was characterized across studies. Several studies reported RRs on multiple exposure gradients (such as cumulative exposure, duration of exposure, and intensity of exposure). To handle the heterogeneity of reporting scales and metrics, we applied the following procedure to generate plot 2 for each selected cancer site:

  • Only studies that reported RRs over an exposure gradient were included on plot 2.
  • The RR and CI corresponding to the most extreme category of each reported gradient were abstracted. For example, if a study reported RRs across both probability of exposure and duration of exposure, RRs corresponding to those for whom exposure was most probable and to those with the longest exposure were both abstracted.
  • For studies reporting RRs across several metrics reflecting an exposure gradient, both the highest and lowest reported RRs were presented on plot 2. A pair of summary RRs and 95% CIs was computed, first by including the lowest RRs and then the highest RRs. We view the resulting summary as being robust to variability in the metrics and scales used to report exposure gradients.

Computational Conventions Used for Plot Summaries of Cohort Studies

The RR for a cohort study is the ratio of observed to expected events (for example, observed deaths divided by expected deaths). Information needed to compute estimated RRs and 95% CIs was abstracted directly from the published papers. In many cases, an estimated RR and its CI were reported directly. In other cases, CIs were omitted and needed to be computed from available information; we used the following conventions:

  • In several studies, the authors supplied incomplete information (for example, RR and observed cases but not expected cases). Whenever two pieces of information were supplied, we calculated the third.
  • In many other studies, an RR was given but no CI. However, the CI could be readily obtained from observed and expected counts by using Byar’s approximation, which has been shown by Breslow and Day (1987, page 69) to be very accurate.
  • In the uncommon situation in which the RR was given with only a p-value (without observed or expected cases and without a CI), we used the following procedures to recover the CI:
    • — When only the point estimate and a p-value were given, the CI was computed by inverting the hypothesis test, as follows. Suppose p denotes the p-value from a two-sided hypothesis test. Let Zp/2 denote the ordinate that cuts off probability p/2 in the right tail of a standard normal distribution. Then se[log(RR)] = log(RR)/Zp/2, and the associated 95% CI for the RR can be computed by exponentiation of log(RR) ± 1.96*se[log(RR)].
    • — When an upper bound for a p-value was given (such as p < 0.05), we made the conservative assumption that the p-value was equal to its upper limit (such as p = 0.05) and computed the standard error (se) as above. (The true CI is narrower than the one derived here.)
    • — When a lower bound for a p-value was given (such as p > 0.05), we plotted the RR but did not calculate a CI.
  • In some cases, RR was zero (the number of expected cases was positive, but the number observed was zero). These cases were entered on the plot with an arrow indicating that the lower confidence bound is at negative infinity; confidence limits were not calculated. These cases were included in the summary RR derived via Poisson regression.

Summary Plots for Case-Control Studies

Organization of Summary Plot

Odds ratios (ORs) were abstracted from the case-control studies as the estimate of cancer risk. Given the relative rarity of the cancers under consideration, those estimates of risk may be considered equivalent to RRs (Koepsell and Weiss 2003, Rothman and Greenland 1998), and so a distinction will not be made between ORs and RRs in the remainder of this report.

Two sets of plots were constructed for each cancer site. Table 2.3 summarizes the organization of plots for the case-control studies at each cancer site. As with the cohort studies, for each of the plots described here, a 95% CI for the weighted average of the RRs is given below the individual study values. For plots with stratification, the aggregate RR and CI are included for each stratum. All the case-control studies that met the committee’s criteria for inclusion in the quantitative evidentiary database reported findings exclusively for cancer incidence.

TABLE 2.3. Organization of Summary Plots for Case-Control Studies Informative for Cancer at Each Site.

TABLE 2.3

Organization of Summary Plots for Case-Control Studies Informative for Cancer at Each Site.

The first set of plots characterizes the effects of any exposure vs none. Plot 1a includes every study, without reference to study characteristics (exposure ascertainment method and confounder adjustment). Plot 1b is stratified by EAM, where “EAM = 1” indicates higher quality exposure assessment as described previously and “EAM = 2” indicates a lesser quality of exposure assessment. For studies of laryngeal and pharyngeal cancers, we included a third plot (1c) stratified on whether adjustment was made for smoking and alcohol consumption. For other sites, the small number of studies did not permit similar stratification.

The second set of plots characterizes extreme exposure vs none with data from those studies that reported exposure effects on a gradient; we used the same approach applied to cohort studies.

Computational Conventions Used for Plot Summaries of Case-Control Studies

For each study population represented in the plots, its estimated RR and its 95% CI or standard error were abstracted as available from the manuscripts. In most cases, the estimated RR and its CI were obtained directly. In cases in which CIs were not presented in the articles, they were computed if possible from available information:

  • In the uncommon situation in which the RR was given with only a p-value, we used the procedures described for cohort studies to recover the CI.
  • In the small number of cases in which the estimated RR was zero and no CI was given, we used the standard method of adding 0.5 to each cell in the two-by-two table of case status vs exposure status and calculated the CI by using formulas supplied by Agresti (2002).
  • A small number of studies reported an adjusted RR, but neither a p-value nor a CI. For those cases, we compared the crude RR (computed from information usually available in a table giving the total number of cases and the number of cases exposed to asbestos) with the adjusted RR. If the crude RR was within 1 standard error of the adjusted RR, we calculated and used the CI for the crude RR.

Computation of Summary RRs

For each plot (and within each stratum for stratified plots), an estimated aggregate or summary RR and its associated 95% CI are given. An outline of the calculation of those values for cohort and case-control studies follows.

Cohort Studies

In a cohort study, the number of observed events (such as observed deaths) can be assumed to follow a Poisson distribution with the mean equal to the expected number of events in the absence of an exposure effect (such as, expected number of deaths), inflated by the true RR (Armitage et al. 2002). This suggests the model:

Image p2000f62eg42001.jpg

where for study j, Yj denotes observed number of cases, Ej denotes expectednumber, and exp(θ) is the average RR across studies.

To estimate θ and its confidence interval, we fit the Poisson regression:

Image p2000f62eg42002.jpg

to the observed event counts across studies, treating θ as an offset term. The standard error calculation took into account extra Poisson variation by using the estimated deviance. The resulting summary RR and its CI for each plot are given by:

Image p2000f62eg42003.jpg

Case-Control Studies

The summary RR and CI for case-control studies was computed with the method of DerSimonian and Laird (1986). That approach assumes that the distribution of true log RRs across studies follows a normal distribution with mean θ and variance σ2. The average log RR is computed as a weighted average over studies, where the weights are inversely proportional to the standard error for each estimated log RR (therefore, larger studies contribute more information).

Let θj represent the estimated log RR reported from study j, and let sj denote its standard error. The logarithm of the summary RR is computedby using a weighted average:

Image p2000f62eg43001.jpg

The weights are given by:

Image p2000f62eg43002.jpg

where σ^2 is an estimator of the between-study variation in the true log RRs across studies. (The DerSimonian and Laird estimator uses a moment-based procedure to compute σ^2.) The standard error of θ^ is:

Image p2000f62eg43003.jpg

Therefore, the lower and upper 95% confidence limits for the summary RR are given by:

Image p2000f62eg43004.jpg

INTEGRATION OF DATA

Previous evaluations of specific agents or exposures as contributing to an increased risk of cancer have been conducted by expert panels convened by national and international agencies. The expert panels review, evaluate, and integrate the scientific evidence based on three sources of information: epidemiologic studies of cancer in humans, studies of cancer in experimental animals, and biologic mechanistic data. The present committee critically reviewed and summarized the strengths and weaknesses of the scientific evidence of those three types, guided by the newly revised principles and procedures described in the preamble to the IARC monographs (IARC 2006).

Such guidelines for causal inference are not rigid criteria that can be implemented in a formulaic fashion, so the committee endeavored to achieve comparability across the cancer sites in the application of the criteria it had adopted by following a uniform format for the critical, final sections of Chapters 7 through 11. The concluding section for each site documents the extent of the epidemiologic evidence from the comprehensive search that proved informative for that site, the consistency of that evidence, and the strength of association conveyed by it. The epidemiological evidence was integrated with the complementary evidence on dose, mechanisms, and toxicologic research. All conclusions were made in accord with the prespecified classification for causal inference.

Exposure Data and Epidemiologic Evidence

The committee considered the geographic distribution, commercial applications of asbestos fibers, and exposure data from occupational and environmental sources. The quality of exposure data and the demonstration of dose-response relationships in human epidemiologic studies were major considerations in evaluating the studies. Other considerations used to assess quality included bias and confounding, as discussed above. In addition to case-control studies and cohort analyses, the committee considered a small number of human case reports that examined biomarkers of potential adverse effects of asbestos fibers and dose deposited at target organs that may be relevant for development of cancer at the sites under consideration. The strength of the epidemiologic evidence for a casual relationship between asbestos exposure and development of cancer at each site was distilled, as described above.

Studies in Experimental Animals

The committee reviewed all animal studies published in the peer-reviewed literature related to asbestos exposure and development of cancer at the sites under consideration. Those studies were evaluated qualitatively and quantitatively according to the criteria outlined in the preamble to the IARC monographs, as summarized in Table 2.4.

TABLE 2.4. Evaluation of Animal Studies.

TABLE 2.4

Evaluation of Animal Studies.

Biologic Mechanistic Data

The committee reviewed the current mechanistic hypotheses regarding asbestos-related diseases of the lung and pleura. From the information on pulmonary diseases, the following properties of asbestos fibers were considered to be most relevant for pathogenicity: fiber length and diameter, surface reactivity, cytotoxicity, genotoxicity, and persistence at the target site, in that they might contribute to chronic inflammation and cell proliferation. The evidence for fiber deposition, persistence, and induction of mor phologic, cellular, or molecular changes relevant to carcinogenicity at the sites under consideration was evaluated.

The committee evaluated the overall strengths and weaknesses of the scientific evidence based on human epidemiologic studies, animal studies, and biologic mechanistic studies. It then integrated all this information before reaching a conclusion regarding the strength of the evidence for a causal association between asbestos exposure and an increased risk of cancer at each site under consideration. Integration of this evidence—reflecting the consensus reached by the committee—is summarized at the end of each site-specific review.

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Copyright © 2006, National Academy of Sciences.
Bookshelf ID: NBK20327

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