For many people, the COVID-19 pandemic was the first time they’ve been exposed to the idea of an uncontrolled disease—introducing phrases like “transmission,” “incubation period,” “contact tracing,” and “herd immunity” into the public vernacular. But for those in the field of epidemiology, these ideas are at the core of their careers, and a pandemic is exactly what they’ve been preparing for. Epidemiologists have historically performed vital work to protect and improve the health of populations, whether it is neighborhoods, cities, countries, or continents. Show Epidemiologists are crucial in mapping and understanding the effects of the coronavirus, but their work extends beyond novel viruses and pandemics. So, what is this unique field? And how do epidemiologists approach issues in public health? What is epidemiology?Epidemiology is the foundation of public health and is defined as the study of the “distribution and determinants” of diseases or disorders within groups of people, and the development of knowledge on how to prevent and control them. Epidemiological research helps us understand not only who has a disorder or disease but why and how it was brought to this individual or region. One of the earliest instances of modern epidemiology can be found during an 1854 cholera outbreak in London. Doctors believed the widespread illness must have been airborne, but Dr. John Snow, widely considered to be the father of epidemiology, employed a different kind of thinking. By carefully mapping the outbreak and analyzing those who were infected, Snow was able to link every cholera case to a single water pump at the intersection of Broad and Cambridge Streets (now Lexington Street) in London’s Soho neighborhood. The removal of the pump stopped the disease in its tracks—laying the basis of today’s epidemiological practices. Today, epidemiologists use the insights gathered in their research to determine how illness within a population affects our society and systems on a larger scale, and in turn, provide recommendations for interventions, such as removing a fatal water pump. As the novel coronavirus became widespread, epidemiologists around the world worked to control the spread. Our research spans work to better understand the virus and how it is transmitted; to project its spread and identify vulnerable communities; to develop diagnostic tests and therapies; and, to assess the U.S. and global health systems’ preparedness. See examples of our faculty's work with COVID. Types of epidemiologyEpidemiology can cover a wide range of issues, from unintentional injuries to psychosocial stress. Here are a few areas in which Columbia Mailman faculty and students work:
How epidemiologists track diseasesEpidemiology centers around the idea that disease and illness do not exist randomly or in a bubble. Epidemiologists conduct research to establish the factors that lead to public health issues, the appropriate responses, interventions, and solutions. By using research—from the field and in the lab—and statistical analysis, epidemiologists can track disease and predict its future outcomes. In the case of COVID-19, this analysis requires heavy data surveillance, collection, and interpretation. Data Due to the scale and threat of the coronavirus pandemic, testing centers, and healthcare systems are required to report all related data, providing epidemiologists with a wealth of information upon which to base their studies. With this information, epidemiologists will track data including:
Epidemiological Modeling Using this data and more, epidemiologists create models that help predict the spread of the disease in the future—including where and when the spread may occur. They may also be able to discern the most vulnerable populations likely to contract a disease and provide recommendations for intervention. See examples of our faculty's work modeling COVID data. Contact Tracing In an attempt to stop the spread of disease and understand where it might go next, many public health workers use contact tracing to determine the connections of an infected person. See what some of our students have been doing: Students take the lead on the COVID-19 response. Degrees in epidemiologyBy achieving a degree in epidemiology, you are poised to work in places such as local health departments, nonprofits, government organizations, academia, the pharmaceutical industry, and more. With Columbia Public Health programs ranging from MPH, MS, DrPH, and PhD, students at all levels can gain the necessary knowledge to drive public health initiatives and conduct independent epidemiological research. Our graduates go on to work in roles at companies and organizations ranging in size, scope, and mission, such as:
Other areas of employment among our graduates include:
The Department of Epidemiology at Columbia University Mailman School of Public Health is committed to producing world-class science with real-world impact while training the next generation of epidemiologists to improve the health and lives of communities around the world. Apply today or explore our overview book for more info.
The basic epidemiological study designs are cross-sectional, case-control, and cohort studies. Cross-sectional studies provide a snapshot of a population by determining both exposures and outcomes at one time point. Cohort studies identify the study groups based on the exposure and, then, the researchers follow up study participants to measure outcomes. Case-control studies identify the study groups based on the outcome, and the researchers retrospectively collect the exposure of interest. The present chapter discusses the basic concepts, the advantages, and disadvantages of epidemiological study designs and their systematic biases, including selection bias, information bias, and confounding. Keywords: Bias; Case-control study; Cohort study; Confounding; Information bias; Observational studies; Selection bias; Study design. Choosing from among different possible study designs to assess cancer risks in populations near nuclear facilities, or even deciding against making a proposal for a particular study design, is based on answers to several difficult questions. Most of these questions are scientific, dosimetric, epidemiologic, and statistical, and require technical knowledge and expertise. However, some are less technical and involve public concerns and perceptions that may be difficult to quantify. The primary focus of this chapter is on technical issues, partly because they serve as a foundation for judgments that may involve additional public and stakeholder considerations. The committee considered the following general approaches to an epidemiologic study of cancers that might be undertaken by the USNRC: The discussions of these possible studies in the following sections are based primarily on the study characteristics summarized in Table 4.1. Section 4.2.1 of this chapter considers matters that affect most or all of these study designs; Section 4.2.2 describes each approach in some detail. These descriptions define the strengths and weaknesses of the recommended studies, summarized in Section 4.2.3. Section 4.3 provides a summary of data sources for population counts, health outcomes, and other information required for the execution of the studies considered and recommended. In any of the studies considered, population sizes, estimated doses, and resulting risk estimates may be too low to demonstrate statistically significant increased cancer risks near nuclear facilities. As noted in Chapter 3, the dose received from living near a nuclear plant is estimated to be less than 0.01 mSv/yr (USEPA, 2007). This dose is much lower than doses from natural background radiation and medical diagnostic procedures, which combined are estimated to be 6.2 mSv/yr for the average2 person in the United States (NCRP, 2009). Consequently, the attributed risk to exposure from radiation from a nuclear facility, if any, would be a small increase above the baseline lifetime risk of cancer occurrence in the general population in the United States, which is considered to be 42 percent (NRC, 2005). Statistical power calculations based on estimated exposure estimates indicate that extremely large sample sizes are required except under the following scenarios: A.Routine releases from the operating facilities have been far greater than those reported to the USNRC, or B.Sensitivity to radiation as characterized in most or all generally accepted risk models is either inappropriately low or simply irrelevant to the populations living near nuclear facilities in the United States. Regarding scenario B, underestimation of risks associated with radiation could be perhaps a result of inaccurate models for interpolation to low doses. Translation of risk estimates from World War II atomic bombing survivors to the population in the United States may also be proven inaccurate, though there is reasonably good concordance of estimated risks for Japanese and Western populations (UNSCEAR, 2006, Annex A). Exceptions are a few cancer sites with disparate background rates, such as stomach and liver cancer. (These cancers are more common among the Japanese compared to Western populations due to differences in risk factors such as diet and rate of infections.) Even if one or both of these scenarios are considered possible, the reliability of any proposed study still hinges on the technical issues of accurately characterizing doses received by the populations under study over the time of facility operations. Accurate estimation of those doses requires reasonably accurate measures of releases, modeling of exposure levels at various geographic locations, and biologic uptake and biokinetics for ra-dionuclide exposures (see Chapters 2 and 3). Epidemiologic studies provide the most direct and relevant evidence for an association between a suspected risk factor and disease. Each of the study approaches considered in this chapter might produce useful new information regarding the association between living near a nuclear facility and potential cancer risks. However, they are unlikely to contribute substantial scientific knowledge regarding low-dose radiation effects because exposure levels are uncertain and probably low, which produces risk estimates with large relative uncertainties. Moreover, each of the possible study approaches is subject to limitations in the types of questions that may be answered. The committee has framed three questions of primary interest based on its statement of task (see Sidebar 1.1 in Chapter 1): 1.Are any detectable cancer-related health effects, such as mortality and morbidity from any type of cancer, associated with living near a nuclear facility at present or in the past? 2.If so, what are the characteristics of the affected persons (such as age, gender, race/ethnicity)? 3.What are the factors that could (and should) be examined to help detect and adjust for possible confounding (such as smoking and exposure to medical diagnostic procedures)? These questions are closely related, and cannot be fully investigated as if they were independent of each other. The second and third questions are of little interest if there is no health effect to be studied. Furthermore, the difficulties in deriving an unambiguous answer are so great that it seems unlikely that the other questions, as important as they are, can ever be answered with precision by epidemiologic studies of populations living near nuclear facilities. As a result, the committee focused most of its effort on evaluating approaches to address aspects of this first question. If an association between living near a nuclear facility and cancer risk is observed, a balanced “weight-of-evidence” approach needs to be applied to determine whether the association is real, and whether that association can be explained by the radioactive releases from nuclear facilities. A plausible cause-effect relationship between radioactive releases from nuclear facilities and cancer cannot be established solely by examining risks in populations living near nuclear facilities through any of the study designs considered. Direct epidemiologic investigation of the exposures in populations near nuclear facilities is limited by small numbers, the presence of unmeasured risk factors and potential confounders, and/or uncertainty in the exposure estimation. For these reasons, understanding the carcinogenic effects of low-level radiation exposure requires a diverse body of evidence in addition to any epidemiologic findings. Such evidence includes the effects of radiation on cell culture systems and animal models where all conditions including dose and dose rate are easily controlled and measured and therefore causal associations with disease outcome can be established. This is the focus of the Department of Energy’s Low Dose Radiation Program.3 Fundamental to the assessment of cancer risks are the concepts of mortality and incidence rates, that is, numbers of cancer deaths or new cancer occurrences observed or expected per year in a population of a specified size (often presented per 100,000 persons in a population or per 100,000 persons of each gender in a population). Incidence is a measure of disease burden, as it describes the occurrence of new cancer cases. Mortality can index a more severe form of disease burden provided that survival is the same in the groups being compared, as mortality reflects both incidence and survival probability. However, for cancers that are not commonly fatal, for example, thyroid cancer, the most useful end point of disease burden is incidence of the disease since in any given year mortality will represent both new and existing cases of disease. A mortality study of thyroid cancer would have restricted statistical power in testing increases in risk at a certain time and interpretation because most of the incident cases in a year would not be captured in the mortality statistics for that year, and many of the deaths in the mortality data for a given year would have been diagnosed many years earlier. On the contrary, for highly fatal cancers such as lung and pancreatic cancers, mortality data would reflect cancer incidence quite accurately. For diseases that have a greater susceptibility to surveillance bias such as prostate cancer, mortality data may be useful because they are minimally affected by that bias. In an ideal study, one would identify each newly diagnosed case of some cancer type in the population under study at or near the time it was diagnosed. This may be possible in states where cancer registries have been in place for the study period of interest and the data are complete and of good quality (see Section 4.3.2). However, many cancer registries were established after nuclear facilities began operations. The time-limited availability of some registry data would affect mortality studies that use aggregated data at small geographic units such as a census tract; however, it would not affect mortality studies that use aggregated data by county. County-level mortality data have been commonly used in the United States because of the ease of identifying cases nationwide over a long time period through the National Center for Health Statistics (NCHS) (see Section 4.3.3). Misdiagnosis of cancer is currently less of a concern than it used to be for both incidence and mortality studies; however, misclassification4 of cancer types may occur. Moreover, incidence studies may lead to biased results when there are changes over time in the likelihood that a cancer was diagnosed, that it was diagnosed but not reported, or that the diagnostic criteria changed. The likelihood that a life-threatening cancer will not be diagnosed is small, but the prevalence of asymptomatic, undiagnosed cancers, especially in older persons, can be large. Changes in the intensity with which people are screened and cancers are reported and registered (for example, prostate cancer) can produce an appreciable artifactual trend in recorded incidence. Also, the reported site of a cancer may be incorrect, especially in earlier years. An example is the earlier misdiagnosis of metastatic cancers as primary in the brain, whereas newer imaging technologies continue to improve the classification of cancer to the correct primary site. The detection of small, more indolent cancers and the appreciable variation within and between populations in the use of diagnostic tools can affect incidence data but may have little effect on mortality data. Variations in degree of cancer surveillance can be a concern for some cancers; uneven degrees of surveillance in populations in various geographic locales can artificially simulate or mask exposure-response relationships. The primary site of a cancer is more likely to be recorded accurately by a cancer registry than a death certificate (German et al., 2011). Also, trends in registration rates should not be biased by improvements of cancer therapy on patient survival. This problem is avoided by using data on deaths from registries with active follow-up of patients such as that implemented by the Surveillance, Epidemiology, and End Results (SEER) registries (see Section 4.3.2), although such studies would be limited to the states or regions covered by these registries and would not cover all areas near nuclear facilities. For the reasons mentioned above, incidence and mortality studies provide complementary data, and both could provide potentially useful information. When the quality of the incidence and mortality data is high, the mortality-to-incidence ratio is related to case survival; when the quality of one or the other is not adequate, the ratio will deviate from the survival ratio. The value of either incidence or mortality registries increases when data from different times and locations can be compared because they are compiled according to agreed national or international standards. All cancer registries in the United States use classification schemes that are largely compatible with each other and with the classification for causes of death on death certificates. Both risk of developing cancer and risk of dying of cancer are substantial public concerns. In an analysis of cancer risks near nuclear facilities, incidence and/or mortality data are linked with residence at the time of cancer diagnosis or death from cancer that is retrieved from medical records or death certificates, respectively. As cancers manifest themselves years or decades after the exposure (see discussion on latency period in a later paragraph of this section), for such inferences use of incidence data is somewhat preferable to mortality because residence at time of diagnosis is a better indicator of where the person may have lived at time of exposure compared to residence at time of death. Persons who lived in a particular area at time of death may not have been long-term residents of that area and, therefore, may not reflect the address at which the relevant exposure occurred, possibly many years earlier. Radiation can cause cancer in almost any tissue in the body but some sites are more susceptible to radiogenic effects than others (UNSCEAR, 2006, Annex A). In general, it has been found that cell radiosensitivity is roughly proportional to the rate of cell division, so cells that actively divide are more radiosensitive (although there are exceptions to this). Radiation-induced cancers, similar to cancers induced from other risk factors, manifest themselves years or decades after the exposure. The lag time between exposure to a disease-causing agent such as ionizing radiation and the clinical recognition of the disease is known as the latency period. The mean latency period per cancer type due to radiation has not been comprehensively summarized, partly because it varies by age at exposure to radiation (Preston et al., 2002; Ron et al., 1995), type of cancer, and especially duration of follow-up of the cohort. However, studies of the atomic bomb survivors in Japan have demonstrated that for most major cancers the latencies of individual cancer cases begin at some minimum period and extend for the rest of the lifetime. Epidemiologic studies that aim to link exposure to radiation and cancer often use a 2-year minimum latency period for leukemia and a 10-year minimum latency period for solid5 cancers (Boice et al., 2011). For this reason, past exposures are more relevant than current exposures as potential causes of cancer. Given that different segments of the public have concerns about a variety of cancers, study of a wide range of cancers may be necessary, but particular attention needs to be given to the most radiosensitive cancer sites, including leukemia, female breast, bladder, thyroid, brain, and ovary.6 Childhood leukemia is a “sentinel” cancer for radiation exposure and may merit separate, more detailed study with individual exposure information, as will be discussed in Section 4.2.2. Examining cancers that are presumably nonradiogenic in origin such as prostate cancer could serve as useful negative controls. Much of what we know about tissue radiosensitivity comes from studies of the Japanese atomic bombing survivors, who generally received radiation exposure to the whole body. In that population, statistically significant excess risks have been shown for leukemia, non-Hodgkin lymphoma (males only), total solid cancer, and cancers of the oral cavity, esophagus, stomach, colon, liver, lung, skin (nonmelanoma), female breast, ovary, bladder, brain, and thyroid. These results are broadly confirmed by other studies (UNSCEAR, 2006, Annex A). For most other sites data suggest possible positive associations; however, a larger number of cases is needed to reach firm conclusions. The highest relative risks (RR; shown as the estimated RR at a 1 Sv dose at age 70 after exposure at age 30) in the atomic bombing survivors study were: leukemia (RR = 5.3), urinary bladder (RR = 2.2), female breast (RR = 1.87), lung (RR = 1.81), brain and central nervous system (RR = 1.62), ovary (RR = 1.61), thyroid (RR = 1.57), and colon (RR = 1.54) (Preston et al., 2007). For comparison, the risk estimate for total solid cancers was RR = 1.47 (90% confidence interval [CI]: 1.40, 1.54). Two sites were notable for the fact that relative risk after exposure in childhood was much larger than that associated with exposure at age 30, namely, thyroid cancer (exposure at age 10 and age 30, RRs = 2.21: 1.57), and nonmelanoma skin cancer at high doses (greater than 1 Gy) (RRs = 3.28: 1.17) (Preston et al., 2007). Leukemia also showed a higher risk for those exposed in childhood, although the exact excess risk is difficult to estimate because of the complex temporal patterns of risk (Richardson et al., 2009) demonstrated in Figure 4.1. More specifically, excess risk for leukemia varies from >50-fold 5-10 years after exposure, to only roughly twofold by 30 years after exposure; therefore, an average estimate would not correspond to the estimate in various time periods. An epidemiologic investigation of cancer risks due to radiation exposure is complicated by the lack of diagnostic tests, clinical or molecular, that can determine the cause of cancer in an individual. For this reason, it is important to collect, where possible, information on other risk factors linked with the cancer type in question so that investigators can exclude other possible reasons for the disease to have occurred. For some cancers, established risk factors can explain the majority of the observed cases. This is true for lung cancer as smoking causes 90 percent of the lung cancer cases. Given the strong smoking effect, analyzing lung cancer data in relation to low-dose radiation exposure would be fraught with potential problems that would be difficult or impossible to address without accurate historical smoking data for individuals in the study population. For other cancers, however, such as those of childhood, established risk factors that include specific genetic syndromes, prenatal exposure to ionizing radiation, infections, and demographic characteristics such as race/ethnicity, gender, and high birth weight collectively can explain only a small fraction of cases. With the possible exception of purely spatial or purely temporal cluster studies, all environmental epidemiologic studies require some assessment of “exposure” to individuals or groups. This exposure is hypothetical and is used in a general sense (rather than specifically defined by radiation quantity) and could include simply categorizing study subjects into levels based on exposure surrogates as defined below. For studies of cancer in populations near nuclear facilities, there are many different options for exposure classification, ranging from simple proximity of residence at time of diagnosis to the facility to modeled dispersion of reported releases, but “exposure” in such studies has never included detailed personal measurement of radiation for every individual (as it does in occupational radiation monitoring). For details on the studies discussed here, see Appendix A. Table 4.2 lists several definitions of exposure in the literature of radiation epidemiology on health risks of populations living near nuclear facilities. Using examples, the definitions are ranked from a less-defined to a better-defined characterization of exposure. The particular type of exposure used in the design and associated analysis defines the question(s) under study and provides an essential context for interpreting the results of any epidemiologic study. It is obvious that a study with well-defined, accurate exposure data can contribute the most to our understanding of the cancer-associated effects of radiation in the setting examined. The national study conducted by the National Cancer Institute (NCI) and published in 1990 (Jablon et al., 1990; 1991) defined exposure as living in a county in which nuclear facilities are located. This definition is loose because—as pointed out by the investigators—many counties, especially in the West, are large and some are more than 80 km (50 miles) in diameter. For example, the San Onofre plant in San Diego County is located about 60 km (40 miles) from San Diego center. If there was indeed a risk associated with living near the San Onofre plant but the risk is limited to persons living in close proximity to the plant (say, 5 km), the effect would be impossible to detect in a county-based study. This is because the normal cancer rates in the large distant population in San Diego city would dominate the summary statistics for the count and dilute any local effect that might be there (Jablon et al., 1990). An improvement to the 1990 NCI approach is that used in a study in France. Established zones of 20-km radius centered on the nuclear facilities, further subdivided into 0-5, 5-10, 10-15, and 15-20 km zones were used for analysis of cancer incidence in populations residing near the facilities (White-Koning et al., 2004). The German Kinderkrebs in der Umgebung von Kernkraftwerken (KiKK) study used distance of the family’s place of residence from the chimney of the nearest nuclear power plant to define exposure. The distance measurements were established with a precision of about 25 m, although the investigators primarily used and highlighted a distance of ?5 km for analysis (Kaatsch et al., 2008). An isotropic distribution of discharges was assumed (i.e., circular rings of equal exposure around the plant); a more accurate method would model releases according to local topography, wind direction, and precipitation. More graduated rank-order measures of closeness were employed in a British study, using the distance of centroids of census wards from nuclear power plants to define several different types of distance scores as continuous exposure variables. No associations were observed to suggest increasing risk in relation to closer proximity to the plants (Bithell et al., 2008). A recent study in Switzerland (Spycher et al., 2011) also used distance of the family’s place of residence (current or at birth of the index child) to the nearest nuclear power plant as a measure of exposure. Although no doses were actually estimated, an analysis was performed accounting for main dispersal directions of airborne emissions from the nuclear power plants. For this analysis, investigators redefined the exposure as living in a zone around a nuclear power plant that is equivalent in area to a circle with 5-km radius but extends to a distance proportional to the average duration of slow winds (<3 m/s) in a given direction (Spycher et al., 2011). Downwind concentration of radioactive particles has been found to be inversely correlated to wind speed. Evrard et al. (2006) conducted a study using geographic zoning based on doses to the bone marrow estimated due to gaseous radioactive discharges using radionuclide discharge data, local climate data, and a mathematical model of nuclide transfers in the environment. The model was developed by the National Institute of Radiological Protection and Nuclear Safety in France (Morin and Backe, 2002). This ecologic study examined communes (small administrative divisions) located within a 40-km circle around the nuclear facilities in France. The communes were divided into five categories based on the estimated dose. The investigators noted that the categories defined by dose assessments differed from those defined by concentric circles around the facilities due to topographic and meteorological characteristics. Although the estimated doses and distances were significantly and inversely correlated (Spearman’s rank correlation coefficient r = –0.58, p = 10–4), marked variability in the estimated dose within each concentric band remained. The contrast in the mean dose between the lowest and highest dose-based categories (range: 2.11 mSv/yr; ratio: 106) was much larger than the maximum contrast between the concentric bands 0-5 and 15-20 km (range: 1.16 mSv/yr; ratio: 30) (Evrard et al., 2006). This suggests that dose precision and probably statistical power are lost by using only crude distance-based surrogates for exposure levels. The same model to estimate bone marrow doses associated with gaseous discharges from nuclear power plants was used in the recent investigation. This investigation further considered the risks around nuclear power plants in France and included a case-control analysis which had an ecologic element (Sermage-Faure et al., 2012): cases and controls were assigned a single exposure value estimated at the town hall of the commune of residence. A study in Spain performed historical reconstruction of the exposure of the population in municipalities within a 30-km zone from the nuclear facilities or 50-100 km from the facilities as a result of the discharges of liquid and gaseous effluents from the facilities (Nuclear Safety Council and the Carlos III Institute of Health, 2009). Estimated effective dose of the populations of municipalities were reported. The investigators state that upon consultation with the International Commission on Radiological Protection, use of effective dose as an indicator of exposure (created for protective purposes and not for estimation of risk) instead of absorbed doses in individual organs and tissues was deemed acceptable for the epi-demiologic study, provided that the uncertainties and limitations involved were clearly stated. As demonstrated above, studies of cancer risks near nuclear facilities use differing estimates of exposure and commonly suffer from several weaknesses by not accounting for: 1.Prevailing wind directions and speeds or terrain factors, which may appreciably alter exposures to gaseous effluents. 2.Directionality and distance of exposures resulting from liquid effluents, the pathways for which may be narrowly focused geographically. 3.Differences in historic release levels of nuclear facilities, when the pure proximity approach is used and multiple sites are examined. 4.Temporal cumulative exposures or increases in nuclear facility–associated disease risks as the cumulative exposure increases. 5.Temporal and spatial variations in natural background radiation in the vicinity of each site as well as from site to site. In principle, the pure proximity approaches of any study can be improved by incorporating dosimetry information into the risk analyses. Comparison of the study findings regarding the risks in a population using a pure proximity approach to those from an analysis that incorporates reconstruction of the doses received by the same population can prove informative. An example is the recent study in France that showed that children living within 5 km of nuclear plants are twice as likely to develop leukemia compared to those living farther away from the plants. However, analysis of the same population of children using a dose-based geographic zoning approach, instead of distance, did not support the findings. The absence of an association with the dose-based geographic zoning approach may indicate that the observed association of distance and cancer risk may be due to factors other than the releases from the nuclear power plants (Sermage-Faure et al., 2012). Dosimetry models for a geographic unit apply to ecologic studies, where an average exposure is assigned to a population residing in an area (for example, census tract) and every individual in that area is assumed to have experienced this exposure; typically, the smaller the geographic unit the less heterogeneity in exposure per individual, and the more precise the estimated exposure of the populations within that unit. Dosimetry information that takes into account the magnitude and temporal variations of annual releases and the factors that provide directionality and distance variations to those releases provide more accurate estimations of exposure. Operationally, for each geographic unit, an areal centroid can be calculated using Geographic Information Systems (GIS), and the estimated annual organ doses to representative individuals at that centroid point can be calculated. Either the population-weighted centroid or the geographic centroid can be used, depending on whether or not investigators want to adjust for a heterogeneous distribution of people within a given census area. One could use those imputed values in dose-response analyses of health outcomes, including appropriate summations of cumulative radiation dose specific to time, lag times, and age truncation. The same methodology could be used to estimate the doses received by the individuals in a record-linkage-based case-control or cohort study. This implies that each individual is assigned the calculated dose for the census tract within which he or she resides. This leads to loss of statistical power compared to a study in which individual doses are assigned since variability in true dose is underestimated. It is preferred, when possible, to calculate individual doses based on residential address at the time when exposure is likely to be most relevant, such as residence at time of birth for the cases and controls. Calculating individual doses based on the address where the person lived at time of cancer diagnosis may also be relevant to where the person may have lived at time of exposure and likely more relevant than calculating doses based on residence at time of death. An analysis based on residence at time of death is the most likely to be affected by migration bias. Individual dose reconstruction for members of a large case-control or cohort study could be time consuming, especially when the investigator wants to incorporate information on residential history of each individual if this is available through interviews or questionnaires. Information on the approaches for modeling dosimetry data in geographic units is described in detail in Chapter 3. Statistical power is the probability that a study of a specified size and design can detect a predetermined difference in risk in the absence of significant bias, when such a difference actually exists. While the computations can be complex, the concept is simple; higher power to detect effects is better, and if power is too low, a study is unlikely to find a difference of interest even when it actually exists, meaning the study can be shown to be uninformative before it starts and perhaps is not worth undertaking. Thus, a fundamental issue regarding the estimation of risks from low-dose studies is statistical in nature. The sample size required to detect a significant association between dose and an effect is a function of the inverse variance of the dose distribution. In general, as the variance of the distribution of doses increases, the required sample size to detect a particular effect decreases proportionately. This implies that the required sample size (for the exposed group) varies approximately as the inverse of the square of the expected effect size (i.e., N = k / (Effect size)2, where k is some constant). To illustrate this, consider the simple case where there is an exposed group, all with approximately the same degree of exposure, and a very large unexposed group for comparison, and one wished to determine whether there was a difference between the groups in the rate of colon cancer. In this case, variation in the sample size requirements in proportion to the inverse variance of the dose distribution implies that the needed sample size to achieve adequate statistical power (80 percent power is usually taken as adequate statistical power) to see a difference between the two groups varies approximately as the inverse square of the mean dose in the exposed group if the dose-response association is linear. For a hypothetical example, suppose the association between radiation dose and colon cancer risk is linear, and observation of 500 exposed persons for a given period of time compared to a very large unexposed group is needed to have adequate statistical power to detect a radiation-associated colon cancer risk when the mean dose is 0.5 Sv. In the analogue of that scenario, 100 times as many (i.e., 50,000) exposed persons would be required to detect a risk if the mean dose were instead one-tenth as large (i.e., 0.05 Sv), and 5,000,000 exposed persons would be needed if the mean dose were 0.005 Sv. This is graphically illustrated in Figure 4.2, where dose (mGy) versus the required sample size is plotted (Brenner et al., 2003). For doses equivalent to those received by individuals that live near a nuclear power plant in the United States which are estimated to be <0.01 mSv/yr (USEPA, 2007) the numbers of exposed persons required to find a possible association would be truly enormous. Having a range of doses tends to increase the dose variance, so a dose-response analysis would probably have somewhat better statistical power than the simple two-group comparison; but given the typically high correlation between the dose variance and the mean dose in the exposed group, the “inverse square of mean dose” relationship is still a rough rule of thumb that is easier to ascertain and conceptualize than the size of the dose variance. Instead of statistical power to detect an effect, an investigator may want to set bounds on the magnitude of risk. In that case, two different purposes need to be distinguished: 1.If the interest is to establish narrow bounds (i.e., narrow confidence intervals) on the magnitude of risk per unit dose, then a principle similar to that for mean dose and statistical power would apply— namely, a much larger sample size would be required to achieve a given tightness of the bounds on risk per unit dose when the doses are smaller. 2.If the interest instead is to “rule out” a certain magnitude of risk (for example, a 20 percent increase in risk in the exposed group) without reference to their estimated dose levels, then sample size calculations associated with finding a detectable risk per unit dose do not apply. Instead, the calculations involve an estimation of likely confidence bounds given the sample size and anticipated number of cases of the disease (Satten and Kupper, 1990). The latter is usually determined using available disease rates. This second purpose, that is, to “rule out” a certain magnitude of risk, is how the committee based its power calculations. The committee’s aim was to establish the minimum sample size required so that the investigation is reasonably likely to detect an effect of a given magnitude. A 20 percent increase in risk was used as a rough figure that would raise the level of concern in statistical terms (but other alternative scenarios of higher risks are also considered). Similarly, power calculations can be used to calculate the minimum magnitude of the change of risk that can be detected given a particular sample size. To reiterate, calculations of required sample sizes based on current knowledge of the average population exposure of the people in the United States to radiation from the nuclear industry would lead to a small anticipated increase in risk that would require an enormous population size to detect with statistical precision. Even for leukemia, which is considered the most radiosensitive cancer, the expected increase in risk is small. The committee discussed that in the atomic bomb study the relative risk for leukemia was 5.3/Sv dose at age 70 after exposure at age 30. This means that the excess relative risk for leukemia is 4.3/Sv, which is equated to 1.43/100 mSv, 0.143/10mSv, or 0.0143 for 1 mSv. Therefore, the estimate of excess risk that one would be trying to detect in relation to exposures from nuclear facilities would be on the order of 0.000143 or smaller. Such a risk would be virtually impossible to detect for any cancer given the statistical and other variability on the baseline risk. As a result, precise computations of statistical power based on risks due to the expected doses would have little meaning; therefore, computations of statistical power are focused on the population sizes required to “rule out” larger risks. Arguably, the power calculations presented here are based on risks tied to exposures that are on the order of 0.5-1.0 Sv, which are much higher than those expected from the releases of nuclear facilities. On the basis of demographic parameters specified by the committee (U.S. population in 2010 of approximately 300 million, about 15 percent live within 50 km [approximately 30 miles] and 0.3 percent live within 8 km [approximately 5 miles] of a nuclear facility, about 20 percent are children under 15 years of age), the committee calculated the power of several possible scenarios that apply to different study designs using distance from a site as a surrogate exposure measure. The choices of 8- and 50-km comparison zones are used solely to provide a frame of reference for the sample sizes required for adequate performance of an epidemiologic study. These reference scenarios are in general agreement with some published studies (see Table A.2), although often the “at-risk zone” in many of these studies is designed to be slightly closer to the facility (for example, 5 km). As described later in this section a gradient type of analysis rather than an analysis based on two categories is preferred. The scenarios explored are the following: a case-control study with equal number of cases and matched controls (1:1 matching plan), a case-control study with 5 controls per case (1:5), and a case-control study with 100 controls per case (1:100). The latter could approximate the matching ratio of cases and controls of a large cohort study or an ecologic study; as is generally true for rare diseases, far more controls are available than cases in these two study designs. For purposes of this discussion, risk estimations for the different scenarios are presented as relative risks (RR). The odds ratio (OR) calculated for case-control studies (see Sidebar A.1 in Appendix A) approximates the RR from a cohort study when rare diseases are examined. Reporting power calculations based on RR provides a more conservative assessment of power. In these comparisons, the committee made several simplifying assumptions about the relationship between exposure and distance. The committee assumes that: a.Distance to the nearest facility is classified into just two catego ries, for example, living within the 8-km zone (nearest category/exposed) versus living within the 8-50-km zone (farthest and larger category/unexposed) from the nuclear facility. b.Two and one half percent of the population under study is in the exposed category and 97.5 percent in the unexposed category. c.Risk in the exposed category is equal to RR × (baseline risk), where RR is relative risk due to being close to the nuclear facility and baseline risk is the risk in the unexposed category. d.National rates provide the rates of cancer for the unexposed population in the regions under study. e.Distribution of risk factors other than the exposure of interest is nondifferential between the two categories. These assumptions need to be refined if a study is in fact undertaken. Figure 4.3 plots detectable RR as a function of total number, n, of cases for each of the three matching scenarios (1:1, 1:5, 1:100). Detectable RR is defined to be the ratio of risk in the exposed category compared to the unexposed category, for which a study with a given number of cases, n, will have 80 percent power (usually taken as adequate statistical power) to detect the increase at the 5 percent level of significance (one-sided test; see Sidebar A.1 in Appendix A for definition). The detection of RRs that are equal to 1.2 (a 20 percent increase in risk in the 2.5 percent of the study population nearest a facility) with acceptable power (80 percent power) requires that 7,000 to 14,000 cases be recruited (depending on the matching scenario). A 40 percent risk increase can be detected with about 3,800 cases for a 1:1 case-control study and about 1,800 with a case control or a cohort and ecologic study designs of 1:100 matching. Doubling of risk (RR = 2) can be detected with approximately 765 cases and controls for a 1:1 matched case-control study and with about 345 cases with a case control or a cohort and ecologic study designs of 1:100 matching (see Table 4.3 for summary). For rare cancers such as childhood leukemia where the observed number of exposed cases will be relatively small, multiple controls (for example, 5 per case) would help to increase the power of the study. However, the improvements diminish rapidly as the number of controls per case increases, so that 5 compared to 100 controls per case do not increase substantially the power to detect an increase in risk (see Figure 4.2). Another consideration for the design of the study is the number of years of study needed to accrue enough exposed cases so that the study achieves 80 percent power to detect a 20 percent increase in risk of childhood leukemia among the “exposed.” From Figure 4.3, a 1:1 matched case-control study would require about 14,000 cases within the overall study zone in order to have power to detect a 20 percent increase in risk. There are approximately 3,000 childhood acute lymphoblastic leukemia cases diagnosed per year in the entire United States (http://www.cancer.gov/cancertopics/pdq/treatment/childALL/HealthProfessional), 15 percent of which (450) would be in the study zone (50 km from a nuclear facility). Therefore, it would require 31 years of accrual before a study would reach acceptable power. Increasing the number of controls from 1:1 to 1:100 (as in a cohort or an ecologic study) would reduce the needed number of cases to roughly 18 years of accrual. Of course more extreme risks are detectable with much less study accrual time. For example, a doubling of risk could be detected with 350-765 cases or about <1 to 1.7 years of accrual for the 1:100 to 1:1 matched studies. A 40 percent increase in risk could be detected with 4 to 8 years of accrual for the 1:100 to 1:1 matched studies (see Table 4.3 for summary). For most adult cancers the period of accrual required to detect relative-risk increases of these magnitudes is much shorter because of the higher prevalence of disease and the larger population numbers. For example, for breast cancer in women under 50 years of age the national rates are approximately 43/100,000 person-years or about 40,000 women diagnosed per year. Since approximately 15 percent of these women (6,000) are expected to live within 50 km of nuclear facilities this means that it would take around 1-2 years of follow-up to detect an excess risk of 20 percent for this cancer, under the same assumptions as above. The total number of cases and years of follow-up required for the different matching scenarios to detect a range of increases in risk following the assumptions stated above are summarized in Table 4.3. The sample size computations provided here are the bare minimum of data to test the hypotheses at the specified level; thus, a sample size estimate is generally a lower bound on what will be needed, and actual requirements could be much larger. This is because the power calculations presented here are based on simplified models that ignore the effect of other risk factors that are largely unknown at the design stage. Internal pilot data are often used to better inform the power calculations and more reliably estimate the required sample size. Pilot data can account for the patterns of risk factors and potential confounders (if information is available) and the nature of confounding—whether it is positively or negatively associated with the exposure. Power calculations that have not accounted for the effects of risk factors may under- or overestimate the required sample size. Modest improvements in the statistical power can be achieved by examining dose-response gradients, especially when the population under study is exposed to a range of doses (Shore et al., 1992). However, since the mean doses received by the populations near nuclear facilities are expected to be low and the associated risks, if any, are expected to be small, very large numbers of cases and controls would still be required in order for the study to be informative and useful. If the study intends to examine dose-effect relationships, improving the quality of the dosimetry can also afford gains in statistical power. Imprecise estimation of doses can be a source of error that increases the uncertainty in the estimated association, which tends to flatten the dose response and decrease the likelihood of finding a statistically significant association. One way to improve statistical power is to increase the effective sample size. As the time since onset of exposures increases, the follow-up number of the exposed populations increases and the exposed population becomes older. Both of those serve to increase the statistical power to observe potentially elevated risks, the latter because much of a population’s cancer risk is expressed at older ages as the disease rates increase. An additional method to increase sample size is to pool data across numerous studies or study sites. Bias, on the other hand, is not reduced by simply increasing sample size in the absence of other improvements; if larger samples mean that less attention can be given to quality of the individual observations, bias may even increase with sample size. Another way to achieve a more statistically powerful study is to focus on radiation-sensitive end points, that is, those that have shown the largest association with radiation. Leukemia (except for chronic lymphocytic leukemia) has shown the highest radiation relative risks per unit dose of any malignancy in a number of studies, so it is a natural target for study. Other endpoints that show relatively high radiation relative risks are breast cancer in younger women, thyroid cancer in children, and bladder cancer. In mounting a study with an exposed group of a certain size, however, there may be a trade-off between the size of the relative risk and the baseline frequency of the disease in question. If a disease is very rare, even with a high relative risk there may not be enough disease cases to demonstrate an association. On the other hand, with a common disease a relatively low elevation in relative risk may be sufficient for statistical significance. Another strategy to increase statistical power is to concentrate on a “sensitive” subgroup of the population, that is, a subgroup for whom any radiation-associated relative risk may be appreciably higher than for the population as a whole. Efforts are ongoing to try to identify genetically susceptible subgroups of the population and—not surprisingly—research indicates that the DNA repair and cell cycle control pathways may play an important role. To date, however, either the genetic variants are too rare to be studied separately (e.g., in the BRCA1 and BRCA2 genes; women carriers of mutations in these genes are at high risk of developing breast cancer) or to have much impact in general-population studies (Bernstein et al., 2010), or the susceptibility variants show only small elevations in risk and frequently are not replicable. A recent study that examined a set of genetic variants (haplotype approach), as opposed to each variant separately, showed that the risk of acute lymphoblastic leukemia associated with diagnostic irradiation is modified by variants in DNA repair genes (Chokkalingam et al., 2011). The WECARE7 study is examining the interaction between radiation exposure and genetic susceptibility in the etiology of second breast cancer in women with radiation treatment for an initial breast cancer. For genetic sensitivity variables, thus far mostly only rather rare mutations have shown an appreciably heightened radiation effect, which means the number with such mutations among cancer cases nearby to nuclear sites would be very small and not promising for a study (Bernstein et al., 2010; Malone et al., 2010). One sensitive subgroup clearly needs to be considered. A substantial amount of data supports the concept of greater radiation cancer risks after exposure in childhood than after exposure in adulthood. For example, the Japanese atomic bombing survivors data suggest this age differential for cancer mortality or incidence for total solid cancer, leukemia, and cancers of the stomach, breast, colon, bladder, thyroid, skin (nonmelanoma), and a combined miscellany of other sites (Preston et al., 2003, 2007; Richardson et al., 2009). For total solid cancer and a number of the individual sites, the radiation relative risks are roughly 1.5 to 2 times greater for childhood exposures than adult exposures. For leukemia, thyroid cancer, and breast cancer the ratios of relative risks by age at exposure are even larger. In contrast to an investigation that focuses on exposure of genetically susceptible individuals, a study on childhood exposure would affect a significant proportion of the potential study population and therefore has good potential for a study (or for a focus within a broader study). Since the risk of leukemia after radiation exposure at young ages is so pronounced for the first 15-20 years after exposure (Figure 4.1) (Richardson et al., 2009), a study focusing on those with potential exposure who develop leukemia at an early age (e.g., before age 15) might be a relatively powerful study if the doses are high enough. The 0-14 age group has been the target age group for many international studies (see Table A.2, Appendix A). The design of an epidemiologic study of cancer risks around nuclear facilities may include one or few a priori hypotheses to be tested. For example, an epidemiologic hypothesis may be that cancer (all types together or a specific type) occurs more often in populations that live near nuclear facilities than in populations that live further away. Stating the hypothesis precisely, with the method that will be used to test it, is important not only for the collection of the appropriate information, but also because standard statistical techniques require that each tested hypothesis be prespecified; otherwise statistical measures such as p values and confidence intervals lose much of their scientific meaning and become hard to interpret. Statistical issues aside, asking “Does this study yield any associations?” is a poor research strategy (Savitz and Olshan, 1995). If a study has low statistical power and only a small number of disease outcomes is examined (i.e., only a small number of a priori statistical tests is performed), then null (negative) results would be the most likely outcome of those statistical tests. However, when a considerable number of different disease outcomes will be examined, the potential for one or more false-positive results (purely by chance) can become large. If two sets of statistically independent observations are available, each is testing a true null hypothesis, and each is tested at the usual 5 percent level, the probability that the first will be found significant is 5 percent and the same for the second. The probability that at least one will be significant by chance is (1 – 0.95 × 0.95) × 100 = 9.75 percent, almost twice the probability for either test alone. The probability increases further if there are more than two hypotheses. For instance, for independent disease outcomes the probabilities of at least one false-positive result when 10, 20, or 30 outcomes are examined are about 40, 64, and 79 percent, respectively, while the respective probabilities of at least two false-positive results are 9, 26, and 45 percent. In other words, the probability of one of many prior hypotheses yielding false-positive results increases with the number of hypotheses tested. Furthermore, when investigators also examine risks in various subsets of the data (e.g., dose, time, or age subgroups), this also will tend to increase the probability of false-positive findings, especially if particular subsets are chosen because of preliminary inspection of the data to identify “suspected differences.” With a substantially underpowered study, any “positive” finding usually has two characteristics. First, it is likely to be a false-positive finding. Second, it is likely that the risk estimate associated with that positive finding is a large overestimate of the “true” degree of risk (Land, 1980). This can be understood intuitively with a hypothetical, but possible, example. Suppose that, given the mean dose in some underpowered low-dose study, the expected true RRs for a series of health outcomes were about 1.1. However, because of the sample size, the RR would have to be about 2.0 to be likely to be detected as statistically significant. Due to sampling variability, by chance one out of the number of health outcomes might show a “statistically significant” RR of 2.0. The excess for the RR of 2.0 is on the order of 10 times larger than the true excess (that is by chance, an excess of 100 percent when the “true” excess is about 10 percent). In short, “statistically significant” results in low-dose studies where the true risk is small tend to provide falsely exaggerated estimates of risk. Accompanying that is often the common human tendency to focus on the “statistically significant” risks, which means that the false-positive results with large imputed risks get undue attention. The multiple comparison issue would be particularly limiting in the interpretation of the results of an ecologic study in which multiple cancers are examined for individual facilities as well as combinations of facilities, different time periods, and different age groups. Positive associations found by chance are likely to be misinterpreted. In the 1990 NCI study, for example (Jablon et al., 1990, 1991), 3,090 comparisons were made for leukemia after startup of a nuclear facility for different areas and age groups. Nineteen were expected to have a probability below 0.05 by chance alone; the actual number observed was 18. Statistical scientists have various ways of dealing with the multiple comparison problem. One strategy that is sometimes employed to guard against excessive false-positive (i.e., “chance”) outcomes is to use a more stringent level for declaring that some difference is statistically significant. Two such commonly used procedures are the Bonferroni multiple comparison correction and the Benjamini and Hochberg method. However, increasing the stringency for declaring a statistical test as positive has the downside of decreasing the statistical power to detect a real effect. Another way is to examine the number of significant results and look for patterns in them (such as increases in cancer only around a certain type of facility, or in one type of cancer around a number of facilities). A third way is to reexamine the results of the significant tests, perhaps in light of additional data, to see whether there is reason to suspect a real effect. For example, was there a radionuclide released that tends to be carcinogenic to a certain organ, as in the case of radiostrontium and bone cancer? Is the association consistent with other studies of radiation effects and biological plausibility? For example, is an association for female breast cancer more plausible than one for male prostate cancer? None of these, applied in a mechanical fashion provide a sure procedure to distinguish real effects from chance (false-positive) associations, and in the end scientific judgment has to be applied based on such considerations as strength of the study methodology, ability to rule out biases and confounding, and biological plausibility. Confounding refers to an apparent change in the magnitude of the association between the exposure (e.g., radiation) and some outcome (e.g., lung cancer) that comes about because of associations with a third, “confounding” variable. Confounding variables might be exposures to toxic or preventive agents, lifestyle or dietary variables, or other disease risk factors. An important statistical concept regarding confounding is that the degree of confounding of the exposure-outcome association depends on the degrees of association of the potential confounder variable with both the exposure and the outcome, as well as the strength of the exposure-outcome relationship. The term “confounding” is frequently used without careful consideration of the true definition to describe the differential distribution of characteristics of the groups under study (for example, between cases and controls, exposed and unexposed). So, for example, if there is an empirical association between the potential confounder and the outcome, but no association between the potential confounder and the exposure, there will be no confounding. Likewise, an association of the potential confounder with the exposure but not with the outcome will mean there is no confounding. (In actual studies it is typically not an all-or-none situation, but a matter of degree, depending on the magnitude of correlations of the confounder variable with the exposure and outcome variables.) Issues of confounding are important in all epidemiologic studies with no exception, and they are particularly important in low-dose radiation studies that examine rare diseases, as even a small degree of confounding can distort the study results substantially and produce incorrect results. An observed small relative risk such as 1.2 (a 20 percent increase in risk) is more likely to be a result of methodological flaws than a relative risk of 5 (fivefold increase in risk). Confounding can create erroneous risk estimates that either exaggerate or nullify the true degree of association. Studies of health effects associated with high levels of radiation exposure usually are not affected by major confounders, because confounding by other exposures or risk factors tends to be considerably smaller than the radiation effects in question. However, with low-dose studies in which the size of the radiation effect is expected to be small, the magnitude of potential confounding effects may be as large, or larger than the size of the radiation effect. In that circumstance, there is a potential for a substantial degree of confounding of the exposure effect. Insofar as studies do not have information with which to evaluate particular variables that might be confounders, potential confounding is a source of uncertainty that can make low-dose study effects difficult to interpret. When information on the potential con-founders is available, adjustment8 for them can be made in the statistical analysis to help remove their effects. Smoking is an example of a serious possible confounder for lung cancer because of the very strong causal relationship between smoking and lung cancer. (Smoking can also be a confounder for other cancers such as bladder cancer.) Small differences in smoking habits can have a greater influence on lung cancer risks than do differences in exposure to low levels of radiation; the relative risk of lung cancer associated with cigarette smoking for moderate to heavy smokers generally exceeds 10, while the RR associated with exposure to high doses of radiation rarely exceeds 2 (Pierce et al., 2005). Therefore, collecting detailed information on the individuals’ smoking history (number of cigarettes smoked per day, age of smoking initiation, years of smoking) is crucial as even slight variations in smoking patterns can bias the results. If the information is not available, it is almost impossible to determine that radiation exposure increases one’s risk of developing lung cancer even if data suggest that. An ecologic study that uses aggregate health survey data on smoking is not expected to provide adequate adjustment for potential confounding by smoking because it is unable to capture specific smoking patterns or the complicated interactions between smoking and socioeconomic factors. This inability of ecologic studies to properly adjust for confounding often leads to hesitation of the scientific community to embrace results and outcomes of these studies. An example already discussed is the large county-based ecologic study in which a decrease in lung cancer mortality was observed in association with increased radon exposure in sharp contrast to the increase expected from current knowledge (Cohen, 1995, 1997). Subsequent investigators who reviewed the data were skeptical as to whether confounding by smoking was properly adjusted for (Heath et al., 2004; Pawel et al., 2005). Indeed, a series of studies using estimated individuals’ radon exposure have shown positive associations (Darby et al., 2005). If the likely confounders have been measured in the study, one way to control for confounding in the design stage is to match9 on one or more factors about which the investigator is concerned that would distort or confound the relationship between exposure and disease under study. Matching has been defined as “the process of making a study group and a comparison group comparable with respect to extraneous factors” (Last, 1995). This way, there will be identical confounder distributions among cases and controls or exposed and unexposed groups. Matching is more often used in case-control than in cohort studies and can occur at the level of the group and is then called group or frequency matching or at the individual level and is called individual or paired matching. Although matching for factors may appear to be a tempting way of controlling confounding, adjusting for confounders inappropriately can result in “overmatching.” Overmatching can occur when investigators match for a variable that is correlated with the exposure of interest or is connected with the mechanism whereby that exposure affects the disease under study. If the confounding factors have not been measured, the data may be misleading and findings need to be interpreted with caution. If a confounder is measured imperfectly due to missing information, classification of the confounder is too broad, or the confounder is misclassified, confounding may still exist, and it is termed residual confounding. A valuable strength of an epidemiologic investigation of cancer risks that incorporates dose reconstruction stems from the fact that the population of interest is examined directly for cancer occurrence or death from cancer; no extrapolations are required from other human populations exposed to high doses, or acute doses, or from animal or cell studies that would add various uncertainties in the risk estimations. (The risk projection model described in Section 4.2.2 is not considered to be an epidemiologic investigation.) Still, any of the study designs considered would attempt to demonstrate very small radiation effects, if any, associated with low doses, and would deal with particularly challenging problems related to uncertainty from various sources. These sources are more often discussed in the context of dose estimations (presented in Chapter 3) and include inaccuracy of measurements used to reconstruct radiation doses, lack of knowledge about true values of dosimetric parameters, and inappropriate assumptions in dosimetric models used to calculate radiation doses to the populations under study. Uncertainty related to the epidemiologic study design itself is often discussed in terms of limitations of the design, analysis, and subsequent interpretation of the findings. Almost any conceivable epidemiologic study must base its analysis on incomplete or imperfect information regarding the population under investigation. Furthermore, some potentially incorrect assumptions, small or large, will be needed, for example, because data are not available or because clarifying the assumptions is not possible. The unknown effects of the necessary assumptions made in analysis contribute to uncertainties in the results. In this section uncertainties are discussed in terms of: a.Completeness of cancer case ascertainment. Cancer risk estimates are based on disease rates obtained from cancer registries and vital statistics offices. Although well-organized means of assessing the quality of cancer registration are in place, at least for the more recent years (see Section 4.3.2), registration is not 100 percent complete or free of errors such as diagnosis misclassification. However, if the frequency of these errors is not large, and not different in exposed versus unexposed areas, the random misclassification should have little effect on the identification of any increased risk. b.Population mobility. Inability to retrieve information on residential history and duration of residence at each location is a major source of uncertainty in the epidemiologic investigation of cancer risks near nuclear facilities. In most such studies investigators estimate the exposure of the individuals or the populations based on one time point: place at time of diagnosis, or at time of death (and the equivalent for controls), or at time of birth. The assumption is that the exposures relevant to the disease occurred while living at that location and that individuals remained at the location of exposure for the period of interest. The issue with this assumption is not only that is likely not true, but also that the results of the study are sensitive to the driving forces that cause people to migrate. Social and economic factors (such as education, job opportunities, and housing) often drive migration and also affect disease outcomes. If migration patterns differ between cases and controls (or between exposed and nonexposed), then the results from the study could be biased. Although it may be possible to quantify the uncertainty introduced by in- or out-migration, exposure from the releases of the nuclear facilities may not be relevant to place of residence but more to place of employment for the adult working population. As an example, take a person that lives 60 km away from a nuclear facility (outside the zone of interest of 50 km that has been discussed in this report) but works 10 km from a nuclear facility or in a nuclear facility. This exposure misclassification is impossible to capture without enquiring detailed information on both residential and employment history through interviews and questionnaires. A study of young children (for example, 0-14 years of age) is likely the least affected by the issues related to migration and/ or place of exposure misclassification. Young children would not only have less opportunity to migrate, but they would also tend to spend more of their time at home compared to adults whose work or other activities may be taking them elsewhere. Additionally, a study of young children where analysis is based on birthplace (rather than place of diagnosis or death and the equivalent for the controls) could capture exposures of the child’s early life and exposures of the fetus during pregnancy, two periods during which humans are particularly sensitive to the effects of ionizing radiation (Pierce et al., 1996). This said, studies of young children are not immune to the impact of mobility or exposure misclassification. A surprising number of families move during pregnancy (Fell et al., 2004) and more than 50 percent of children ages 3-6 are enrolled in center-based care (http://www.childstats.gov/americaschildren/famsoc3.asp). Arguably, a study of the cancer risks of populations near nuclear facilities (especially of the older populations) that is based on place of death is more affected by migration bias. There are, however, good reasons to perform combined analyses of mortality and incidence for reasons described in Section 4.2.1. c.Variability in risk factors. There is inherent variability in the characteristics of the populations in an epidemiologic study that include variability in their genetic make-up, susceptibility to cancer, lifestyle factors, and personal habits. These factors are not easily measurable even if detailed interviews are conducted and/or biological samples are taken. In a low-dose epidemiologic study, the magnitude of the variation in these unmeasured factors may surpass the expected effect from radiation released by the nuclear facilities and therefore obscure any actual effect attributed to the radiation. The variability in population characteristics would not have as profound of an effect in a high-radiation-dose epidemio-logic study because the excess risk tends to be greater than most variation in the baseline risk. d.Inability to distinguish risks from different sources of radiation. Similar to the “noise” on baseline cancer risk that arises from the variability of risk factors such as those discussed above, variability in exposure to other sources of radiation is difficult to measure with accuracy. An increasing source of radiation dose to the population in the United States is from exposure to medical diagnostic procedures, which accounts for almost half of the annual dose that the population receives (NCRP, 2009). In the current context, collecting information on frequency of high-dose procedures such as computed tomography (CT) exams or doses received from these procedures is important as these doses are much higher than those expected to be received from routine operations of the nuclear facilities.10 In the absence of a national system that tracks population utilization and exposure to medical procedures that involve radiation use, retrieving the information on medical imaging utilization is not possible unless medical charts are reviewed or personal interviews are conducted; then the potential for collection of inaccurate information or recall bias is a concern. As the methods to obtain organ dose are not fully developed yet, calculating the doses to the exposed populations per imaging modality, if possible, would introduce additional uncertainty. e.Potential confounding. A risk factor such as smoking or exposure to medical diagnostic procedures has to be formally tested to assess whether it is a true confounder or not under specific circumstances. Smoking is of particular interest because as discussed in the previous sections it has the potential to be a serious confounder for lung cancer and other cancers such as bladder cancer. However, it is often not possible to collect accurate and detailed information to fully test for confounding. f.Synergistic and antagonistic effects with radiation. Collecting information on lifestyle factors and exposure to agents such as toxic substances is also important for the examination of synergistic or antagonistic effects with radiation. A collaborative multicountry study in Europe aimed to determine the risk of lung cancer associated with exposure to radon at home. Results demonstrated that residential exposure to radon among smokers and recent former smokers increased the risk of lung cancer compared to individu als who did not smoke currently or in the near past (Darby et al., 2005). Similar interactions may exist between radiation and inherent characteristics of the individuals such as genetically based inability to repair damage from the exposure. A review of the literature on the interaction between genetic susceptibility and radiation on cancer risk is presented elsewhere (UNSCEAR, 2006, Appendix A). g.Use of proxies. Although proxy measures in general are often accepted indicators of an exposure and can prove informative, there is uncertainty as to whether the exposure of interest has been sufficiently investigated by the use of that proxy. The uncertainty varies with the degree of “closeness” between the proxy and the real measure. For example, high socioeconomic status and educational level are often used as a proxy for a healthier lifestyle and access to health care. Birth order11 and day care use during infancy (Law, 2008) are often used to measure frequency of infection in children. These proxies have been used by a recent study of risks in populations near nuclear facilities (Spycher et al., 2011) to adjust for confounding linked with the “population mixing hypothesis” that has been applied to explain observed leukemia clusters around nuclear facilities in Europe, such as that around Sellafield in Britain (Kinlen, 2011). According to this hypothesis, childhood leukemia is a rare response to common infection, which may be introduced to a previously isolated rural community by sudden in-migration and changes in the dynamics of infectious diseases. Simply, when a population is mixed with another population that has not previously been exposed to the infectious agent (yet to be identified), individuals in the previously unexposed population may develop the disease. h.Statistical uncertainty. There are inherent statistical variations in fitting dose-response models. It is important that uncertainties be incorporated properly into risk calculations and be communicated clearly. Interpretation of risk estimates is also based on uncertainties from less than perfect knowledge of the effects of low-level radiation on human health. The value of a study increases if it is performed in the context of existing investigations, and if its results are supported by other studies in the field. To evaluate the potential cancer risks associated with living near a nuclear facility directly requires very large-scale studies (Land, 1980) and still it would be extremely difficult to estimate the health effects by studying the exposed populations alone. This is because at very low doses, the radiation-related excess risk tends to be buried under the noise created from statistical and other variation in the baseline lifetime risk of cancer which in the population of the United States is estimated to be 42 percent (NRC, 2005). A more timely risk assessment can be obtained using risk-projection models. Risk-projection models would involve using dose data related to the exposures of individuals living near nuclear facilities and quantifying the risk by transferring that observed in other exposed populations. Data from the Japanese atomic bombing survivors’ cohort are most often used for the purposes of assessing the risks arising from exposure to radiation. This is because this cohort has the most detailed information available for most cancer sites. The models for breast and thyroid cancer are often based on pooled analyses of the Japanese and Western populations such as those that were medically and occupationally exposed (see Appendix A for literature review). These models would calculate a theoretical excess risk of cancer for the populations near the facilities by using the most relevant risk estimates and interpolation models, as well as population characteristics like age structure and population mobility. Then one can produce estimates of changes in risk, or demonstrate that any increase is smaller than some upper limit. If the upper limit is an “acceptable” level, then the true level of risk associated with living near a nuclear facility which by definition is lower than the upper limit is unlikely to be unacceptable (Land, 2002). Such a method was used to project the cancer risks associated with exposure to radiation from other sources such as the use of CT scans and to assess which age groups were associated with the highest risks (Berrington de González et al., 2009). Organ-specific doses and frequency of CT use were derived from national surveys. The investigators discuss that they used this indirect modeling approach to provide more timely risk projections; otherwise, long-term follow-up of very large populations would be required. There are limitations associated with the use of risk-projection models to transfer risks from more heavily exposed populations such as the Japanese atomic bombing survivors to the populations in the United States that receive much lower doses estimated from reported releases from each facility to be studied. First, the baseline cancer rates of the comparison population (i.e., Japanese atomic bombing survivors) are often different from that of the population of interest (i.e., residents around nuclear facilities in the United States), and for a few cancers such as breast and stomach cancer the relationship between radiation-induced and baseline risk may differ (UNSCEAR, 2006, Annex A). For example, the age-adjusted incidence rate for breast cancer is 34 per 100,000 per year for Japanese women and 90 per 100,000 per year for the women in the United States (Parker et al., 2002). Breast cancer has occurred in excess among women survivors of the atomic bombings in Japan and among those exposed over many years to medical radiation in the United States. The excess relative risk of breast cancer incidence in the Japanese atomic bombing survivors, however, is significantly higher than that of medical radiation patients in the study in the United States (Little and Boice, 1999) and the best estimate of the ratio of the excess relative risk coefficients for the Japanese and U.S. cohorts is about 2. However, this higher relative excess risk is attributable to the lower baseline risk of breast cancer among Japanese women compared with the women in the United States. The excess absolute breast cancer risks in the two populations are statistically indistinguishable (Little and Boice, 1999). Related to this difference in baseline cancer rates and the relationship between radiation-induced and baseline risk is the question of whether relative or absolute transfer of risks between populations is the most appropriate (see Sidebar A.1 in Appendix A for discussion on risk measures). Second, additional assumptions are required in risk-projection modeling, which are major sources of uncertainty: sampling variability in parameter estimates in the risk models; the choice of adjustment factors (known as the dose and dose rate effectiveness factor) to use for interpolation from high-dose-rate exposure to much lower dose rates resulting from prolonged releases; and accounting for differences in relative biological effectiveness between different types of ionizing radiation (known as the radiation effectiveness factors). As a standalone study, a risk-projection model would provide less information than the other study designs considered by the committee and described below. A serious problem with such a study is one of public credibility: the calculated dose distribution by necessity must be based on the reported release data—which if drastically wrong, would provide misleading results. Simply said, the accuracy of the risk-projection models is entirely dependent on the accuracy of the reporting of the releases. Noting the concerns above, the committee notes that risk-projection models could provide useful background information in conjunction with the empirical epidemiologic studies discussed in this chapter to provide guidance for dose assessment and to aid in the interpretation of such studies. A main reason why investigators may choose to perform an ecologic study rather than an individual-based study is that the necessary data— depending on the level of aggregation—are routinely available from relevant cancer registries and census bureaus. Hence, it is easier and faster to obtain the aggregated data than it is to collect individual data, the release of which from cancer registries and other relevant offices often involves demanding approval procedures. Because of the relative ease of accessing aggregated data (which is highly dependent on the level of aggregation), multiple disease endpoints in a range of age groups can be studied at once. Despite their inherent limitations, ecologic studies based on cancer incidence or mortality data, even those that focus on large geographic areas such as counties, have proved to be of value in suggesting avenues of research. Ecologic studies are considered as “hypothesis generating” investigations and a finding with possible public health impact will require more rigorous testing using a different study design. As discussed in earlier sections, radiation is associated with elevated risk for a large number of different cancer types and leukemia, female breast, bladder, thyroid, brain, and ovarian cancers are considered the most radiogenic. Given that different segments of the public have concerns about different cancers, an ecologic study that examines the risks associated with a wide range of cancers may be necessary, but particular attention needs to be given to the most radiogenic types. It is important that ecologic studies are conducted using reliable methods and the susceptibility of their research to the ecologic fallacy is clearly described when results are reported. Recent analysis showed that this is often not the case, and the quality and clarity of some publications on ecologic studies is compromised (Dufault and Klar, 2011). The NCI reported an ecologic study of cancer mortality across all nuclear facilities that began operations prior to 1982 and for cancer incidence for two states (Jablon et al., 1991). For the NCI study, the rates observed in the population living in a county containing a nuclear facility or an adjacent county that contained more than 20 percent of the area within a 16-km radius of a facility (exposed) were compared to the rates observed in counties not containing a nuclear facility (unexposed). For every exposed county, three unexposed counties were selected to match on certain demographic factors: percentages of persons in the population over age 25 that were white, black, American Indian, Hispanic, urban, rural, employed in manufacturing, and high school graduates; mean family income; net migration rate; infant death rate; and population size. The analysis assumed that populations living closer to a nuclear facility would receive higher doses of radiation. However, no data regarding radiation exposures or measured releases from the facilities were used in the analysis. That is, the NCI study, similar to other studies of proximity, was not a direct study of health effects of radiation released from nuclear facilities, but rather a study of the health effects of the collection of factors differentiating populations residing near the facilities from those farther away. This includes exposure to radiation but can also include the demographics of the nuclear workforce and the population-mixing hypothesis discussed earlier (Kinlen, 2011). This context is important when considering the role of dosimetry based on reported radiation releases and monitored values from nuclear facilities, especially since the reported doses in recent years fall well below exposures that have been directly shown to cause cancer. The primary analysis in the NCI study compared the ratios of standardized mortality ratios or standardized incidence ratios before and after the date a facility began operation, with the same measures for the matched unexposed counties. Hence, the values were not mutually standardized and are, at best, generic rate ratios. The main focus of the NCI report was on the ratio of pre- and postoperation cancer mortality ratios since appropriate incidence data were only available for two states with long-standing cancer registries (Connecticut and Iowa). Several changes could be made to update and improve the 1990 NCI study design and analysis. Here we discuss five: 1.Reduce the size of the geographic units in the analysis. 2.Use the current nuclear facility inventory. 3.Include years of mortality and incidence data that are relevant to the years of exposure. 4.Incorporate estimated exposure levels for each geographic unit. 5.Use stronger analytic methods that permit direct adjustment for possible confounding variables, and incorporate population mobility and temporal changes in the sociodemographic characteristics of the populations under study. For the first change, reducing the geographic unit to be considerably smaller in terms of physical size, but also in population, for example, using census tracts, allows for a finer distance-based exposure characterization as well as better characterization of the populations that reside within these units such as age, gender, and race/ethnicity structure, and socioeconomic status. As an example of the magnitude of reduction of the geographic size, the U.S. Census Bureau defined 628 census tracts in San Diego County for 2011. This may be one of the most important of these five ways to improve on the NCI study. This approach would also facilitate analyses of risks at a range of distances. Using smaller geographic units in an ecologic study is also a potential strategy to reduce the impact of the ecologic fallacy. Although groups are rarely completely homogeneous, smaller geographic groups can be more homogenous with respect to the exposure under study and possibly other risk factors and potential confounding factors. The strategy of reducing the size of the geographic unit for analysis to reduce ecologic fallacy can also lead to another problem, greater migration between groups (Rothman and Greenland, 1998). For the second change, the inventory of the nuclear facilities in the United States has changed substantially since the NCI analysis; therefore, estimated risks associated with facilities in that study may not be relevant to those operating today. Many nuclear facilities have started operations since 198212 (as the total number of currently operating reactors has increased from 80 to 104), but in some cases these are located at the sites of existing plants within which reactors may have been decommissioned since 1982. Some states that did not have nuclear power plants in 1982 now do (Arizona, Kansas, Louisiana, Mississippi, Missouri, New Hampshire, Texas, and Washington), and some other states that had an operating power plant pre-1982, now do not (Colorado, Maine, Oregon) (see Table 1.1, Chapter 1). For the third change, the follow-up in the NCI study was through 1984 and included facilities that were in operation by 1982. There was very little follow-up time beyond a presumed minimum latency period of 10 years for most solid cancers. (Only with the passage of some years from the year that a facility started operation is it expected that populations living near the facility have accumulated sufficient exposure to develop cancers because of the releases from these facilities.) A current analysis of risks could add 25 or more years (1984-2009) of follow-up. However, an important limitation is the lack of mortality data at the census-tract level: Mortality data that could be readily geocoded to census tract (i.e., addresses are available electronically) do not exist for early years, although data summarized at the county level do exist (see discussion in Section 4.3.3). This recognized limitation of the census-tract-level ecologic design considered here is balanced with the possible gain in statistical power due to the more relevant geographic classification and follow-up period. Many of the 117 plants that are examined in this study (currently operating and decommissioned; see Table 1.1, Chapter 1 for the list) began operations in the 1970s (45 percent) or early 1980s (37 percent), so if mortality data by census tract exist from the mid 1980s onward (with significant variation across states), some 25 years of follow-up would be possible (in some states follow-up would be much shorter, in some longer). Whereas a large fraction of the observation time in the NCI study predated a minimum latency period (of perhaps 10 years after exposure), most of the observation time in this study would occur after the minimum latency period has elapsed. As incidence data in only two states were examined in the NCI investigation (Connecticut and Iowa), the improvements in the incidence analysis are more clear. Moreover, as the year that mortality and incidence data in a state become available varies, the two approaches would provide complementary time coverage. For the fourth change, the level of exposure of populations in specific locations around a nuclear facility is dependent on the magnitude of the releases from the facility, the distance of the population from the facility, the mix of wind directions and velocities, and variations in terrain (for gaseous releases), and the locations and directional flow of liquid releases. All these factors are incorporated in dosimetric models that could be used by epidemiologists to calculate cumulated exposure levels for any given geographic unit, such as a census tract within the 50-km radius from the facility, for each year and perform “dose-response”-type analyses of health endpoints. This would be a substantial improvement over most previous approaches, such as examining a 5-km radius around the facilities. For the fifth change, an overall modeling framework for the analysis of the ecologic data is to develop an extended cross-classification table, each cell of which contains a count of the incident or fatal cases of interest, an estimate of the person-years at risk, and the appropriate estimated exposure quantity and values for other covariates of interest. The cross-classification would be according to geographic unit (for example, census tract, which itself implies the particular nuclear facility under study), calendar year, age, gender, and race/ethnicity. For example, cancer registration of a 50-year-old African American woman, diagnosed with breast cancer in 2005, living in census tract X at the time of diagnosis, would contribute a case count to the cell which records the number of African American women in tract who in 2005 were 50 years old. Census data would be used to estimate the total number of African American women aged 50 years who were living in census tract X in 2005 so that rates can be computed. Other variables available for this census tract at this time would include a calculated dose estimate or dose surrogate, as well as other census data, or data integrated from other sources with census data. These may include estimates of socio-economic conditions prevailing in census tract X in 2005 or at some other time, based on data about education, land use, and home ownership rates. Information about these and other variables may be important because they could act as confounders in the dose-response analysis. For example, breast cancer risk is influenced by factors such as age at first birth, hormonal use and other factors, all of which may depend to some degree on socioeconomic conditions. Poisson regression techniques (described in more detail in Appendix J) would relate the dose surrogates available to the rate of cancer seen in each census tract, after stratifying on race/ethnicity, age, and calendar year, and adjusting for socioeconomic or other variables available at the census-tract level. As population distributions change with time, an ecologic study needs to account for such changes. In the 1990 NCI study, matching of exposed and unexposed counties was based on data for the years 1979 and 1980 (the latest years included in the analysis) and did not consider county characteristics in the 1950s and 1960s, which were likely different from those in 1979. An improvement over the 1990 NCI study would be to allow for differences in cancer rate (incidence or mortality) between geographic regions (census tracts) to depend upon distance or dose as well as time, while adjusting these for the changes in various socioeconomic variables and other risk factors. In addition, dose surrogates will change over time depending on the total cumulative dose that someone living in a given census tract would receive, so that this dose surrogate increases in time as releases accumulate, and the dose surrogate level is specific for time, nuclear facility, census tract, and age (e.g., persons at age 10 in 1990 would not have been exposed to transient plant releases in the 1970s, whereas those at age 30 would have been). The flexible manner of dose assignment to specific cells in the projected analyses could take into account these variations. In census tracts judged to be stable demographically (with few people moving in or out) this could be the most relevant dose function. In other census tracts (with higher in-migration or turnover) early doses may be regarded as less relevant than later doses, and this could be taken into account in various ways. As discussed in Section 4.2.1, dealing with the comparison issue and the expected false-positive findings is especially challenging in ecologic studies where each of the thousands of risk estimations is subject to statistical tests to assess whether any observed association occurred by chance or not. At the end, scientific judgment based on biological plausibility and current knowledge are needed to interpret the findings. Investigators of the 1990 NCI study who based their analysis primarily on a pre- versus post-facility-operation comparison of risks in counties with or without a nuclear facility were able to interpret and communicate the appearance of false-positive findings rather effectively. Data were presented in support of the fact that many statistically “significant” increases in risk in relation to nuclear facilities were found for the period before facilities started operation; these risks could not possibly be attributed to releases from the facilities but are rather statistical effects (Jablon et al., 1990, 1991). The pre- versus postoperation analysis was possible using county-level data as they are available uniformly across the United States and are of good quality. However, reducing the geographic unit to be considerably smaller than a county, which is considered one of the most important ways to improve on the NCI study, comes with the trade-off that risks before the operation of the nuclear facilities can only be estimated for a small number of facilities. These are the facilities that are in states where long-standing cancer registration and mortality data with available information on geocoded address are available for many years. In a cohort study, a defined population is followed forward in time to examine the occurrence of many possible health outcomes. Cohort studies may be either prospective, focused on health outcomes occurring after the start of the study, or retrospective, using existing data in registries to construct a cohort and follow it forward to the present and sometimes beyond. Disease incidence in individuals who are “exposed” are compared to those who are “unexposed.” Prospective cohort studies in which participants are recruited, data on residence locations and various potential confounder variables are collected, and then participants are followed for incident disease occurrence are generally thought to provide the most reliable information about disease risk in relation to a risk factor. The major advantage is that the study can be carefully planned in advance to include such things as individual exposure assessment (e.g., using dosimeters) and other covariate data. Since the exposure data are measured before the cancer occurs, some kinds of biases are reduced or absent, so this cohort design is generally preferred over others for making causal inferences. However, prospectively followed cohorts must generally be observed over a very long time (decades) before enough cases of most diseases are available for statistical analysis. To give one example, atomic bombing survivors, exposed in 1945, were initially interviewed around 1950 and have been followed for mortality outcomes since that time and for incident cancer since 1958. It was not until the 1960s (about 15-20 years after the atomic bomb exposure) that the first statistically significant findings emerged of an increase in solid tumor mortality in exposed survivors (Socolow et al., 1963; Wanebo et al., 1968). A cohort study of the future cancer outcome of individuals near nuclear facilities would involve enormous logistical problems in order to follow individuals for decades into the future. The study would not be able to evaluate past exposures, and this may be a serious problem because the highest radiation exposures may have been in the early years of the nuclear facilities’ operations. Far more individuals than are typically needed for a case-control study would have to be interviewed initially and then tracked in the future for cancer incidence and mortality. Population mobility would mean that such tracking would involve large-scale regional or countrywide efforts. Additionally, to follow a population for many decades in the future as needed in a prospective cohort study relies on long-term institutional commitment that may be difficult to sustain. However, prospective monitoring of populations living around nuclear facilities would provide more accurate estimates of ongoing exposures than those reconstructed retrospectively based on modeling of reported releases from the nuclear facilities. It would also provide data regarding the cancer risks associated with exposures in the future. Retrospective cohort studies, when feasible, are more efficient than prospective studies because the follow-up period is in the past. A retrospective cohort study identifies a group of people at a time in the past for which exposure estimates exist or can be constructed, and follow-up extends from that time to the present. Such designs are commonly used in occupational epidemiology in which workers employed at a particular facility during specific time periods and meeting other inclusion requirements are followed forward to the present for disease incidence or mortality using existing mortality information or cancer registry information. A retrospective study requires that systematic exposure information at the beginning of and during the follow-up period be available from existing records. Exposure information that might be available from company employment records is related to disease or mortality using statistical methods appropriate for time of event analysis (often Cox regression). Other retrospective studies are based on the follow-up of defined birth cohorts and record linkages used to establish both follow-up and exposure. For example, a recent retrospective cohort study of childhood cancer in Switzerland linked birth records with cancer registration data across the country and used the birth and current residential records to determine proximity to nuclear power plants as a risk factor (Spycher et al., 2011). The feasibility of a retrospective cohort study depends upon the ability to define a cohort that will include both exposed and unexposed individuals, to estimate appropriate exposure information passively (that is, without the aid of patient or family contact) from existing records, and to link, also passively, the cohort to cancer registration or mortality records from the time that an individual entered the cohort (e.g., time of birth for a birth cohort) until the end of follow-up. The committee carefully considered the feasibility of a retrospective cohort study of cancer incidence in and around states with nuclear facilities. For the reasons outlined below, only studies of childhood cancers were considered for such a study.
Pediatric leukemia warrants particular attention in the analysis for the reasons summarized at the second bullet point. Similarly, brain cancer, which is the most common solid cancer in children, needs to be given particular attention. Radiation exposure is one of the few established risk factors for this disease. Although all pediatric cancer types can be examined individually, because of the rarity of cancers in children and expected loss in precision in risk estimation it may be needed to create case subgroups based on homogeneity of disease manifestation, etiology, or other categories. The outlines of the study considered are as follows. All reports of childhood cancer in all available cancer registries over a fixed time period would be linked to birth records from states that contain nuclear facilities or are adjacent to nuclear facilities. Nearness to nuclear facilities (or doses from nuclear facilities estimated by the reported releases) at the time of birth would be established using the residential addresses recorded in the birth records. The entire birth cohort would be linked to all cancer registries, not only in the state of residence at time of birth, but also to other state registries, to capture the mobility of the population. Ideally, changes in residence (and hence changes in potential exposures) would be obtained by linkage to databases providing address histories. Dose surrogates would be constructed starting from the time of birth according to residential location. These dose surrogates and cancer incidence data would be analyzed to investigate whether residence patterns that indicated a potential for higher exposure are associated with increased rates of childhood cancers. Although simple to describe, there are many practical difficulties with performing such a study in the United States. These include: 1.Low coverage of cancer registration before about 1992 for most states. 2.The size of the birth cohort required to have adequate power. 3.Lack of information concerning residence changes following birth. 4.Administrative difficulties accessing state birth records databases and cancer records. For more details regarding the first difficulty, see Section 4.3.2. Regarding the second difficulty, Figure 4.3 and Table 4.3 indicate that for a cohort study with a large fraction of unexposed subjects it would take about 1,800 cases in order to have good power to detect a 40 percent excess cancer risk (RR = 1.4) and would require approximately 4 years of incidence data. For example, if all childhood cancers among children aged 0-14 diagnosed in the 4-year time period 2006-2009 were to be targeted in the study (a time when almost all states have working cancer registries), then this would involve linking 18 years of birth records (all children born between 1992 and 2009) to some or all of the cancer registry cases. If we assume that approximately one-fifth of the 4 million births taking place each year in the United States are to women who have home residences within 50 km of a nuclear facility, then this would mean that approximately 14 million birth records would need to be accessible. For the third difficulty, while there are many ways to try to trace people as they change residences (see Section 4.3.5), no comprehensive databases are available, and ad hoc searching for residence changes on a cohortwide basis (for millions of birth records in numerous states with disparate sources of residential information) appears on its face to be prohibitively impractical. This means that the only consistently available dosimetry information would be for the period at time of birth. After that, residential changes would gradually degrade the applicability of individual exposure information, such as estimates of cumulative dose. If one assumed that all individuals remain in the same residence as at birth, then cumulative dose calculations are easy to perform, but developing a more realistic model for the accumulation of dose would involve population-based estimates of the probability of mobility. This may lead to some minor improvements in dose estimation, but the fundamental problem, that it is impossible to trace large numbers of individuals from residence to residence, remains. Despite the inadequacies in the use of birth place as the point of exposure over the follow-up period of interest, it is widely thought that children are the most sensitive to dose received in early childhood or in utero (Pierce et al., 1996), so birthplace may be a more relevant dose surrogate than would be residence at time of diagnosis, as discussed, for example, in the ecologic study. As birth place is defined by maternal residence at time of delivery of the index child it can be used as the point of in utero exposures as well as early life exposures. The mobility of the population during pregnancy remains an issue (Fell et al., 2004). For the fourth difficulty, birth records and cancer registries are typically managed within each state. However, as shown in Figure 4.4d, many nuclear facilities in the United States are located near state boundaries, and populations of interest often reside in more than one state. In addition, the mobility of the population in the United States may also necessitate linkage of registry data across additional states. While not impossible, access to records will require approval from all states involved, creating a logistical barrier to implementation. Going further, although linking birth record data across states may be technically possible, there are anticipated difficulties due to the differences of state statutes governing cancer and birth registration, support to research activities, and concerns about privacy following release of information. All these could decrease the quality of the linkages, lead to failure of linking data across states, and delay completion of the study. The retrospective birth cohort study is judged by the committee to have high scientific merit. However, there are some feasibility concerns at a nationwide scale. A modification of the retrospective cohort study that may be more efficient would be to conduct a record-linkage-based case-control study that is nested in a restricted retrospective cohort study. A case-control approach may be appropriate if efforts are directed to selecting just one or two major diseases that may appear in populations around nuclear sites or are restricted to a specific age group. For example, it may be relevant to focus efforts on studying the risks associated with pediatric cancers developing in young residents close to nuclear facilities or more specifically look at risk factors involved in childhood leukemia developing in this group. The German KiKK study and some other studies have suggested a possible increase of this type of childhood cancer, though many other studies have not replicated this observation (see Section A.4.1 in Appendix A for literature review). Case-control studies using incident (newly diagnosed) cancer cases with data from several registries must consider the years in which registry data are available; the period of inclusion of the cases and controls can be defined once the quality of cancer registration is found to be adequate. Moreover, a case-control study that requires contact with the study participants that is restricted to recent cases (e.g., those diagnosed within the past 5 years) minimizes potential selection biases due to differential disease severity or availability for interview and/or data collection for nonsurvivors. In a case-control study, cases are generally matched to appropriate controls either individually or according to a categorization of variables (often age, gender, race/ethnicity; this is known as frequency matching). In either individual or frequency-matched studies investigators need to determine the ratio of the number of controls to the number of cases, a decision generally driven by calculations of statistical power, and the number of cases expected. For rare cancers such as childhood leukemia, the observed number of cases will be relatively small, and multiple controls (two to five per case) would help to improve the precision of results. However, the improvements diminish rapidly as the number of controls per case increases, and more than five controls per case is not likely to be helpful (see Figure 4.3). It is critical that the number and nature of matching criteria be considered carefully. Overmatching must be avoided; for example, matching closely on place of residence or distance from a nuclear facility may constitute overmatching. That is, investigators “force” the cases and controls to be too similar in the exposure under investigation; therefore, the effect of the exposure on disease cannot be investigated. Obtaining accurate information on past exposures (predating the occurrence of the cancer, or an equivalent time point for controls) can be problematic. If information is to be obtained from existing records, it may be only partly suited to the desired study information. For example, data on smoking might be obtained from employment health records, but the smoking information may be incomplete or too cursory for the need (e.g., “Do you smoke?” rather than detailed information on duration and frequency of smoking, and information may vary across time periods and employers). Records relevant to some exposures would have been generated for administrative rather than medical purposes and therefore might be poor surrogates for the desired information. The information for cases and controls must be collected by the same approach in order to limit bias related to quality of information or extent of detail of the data collected in different administrative files or medical records, or due to differential interviewing. Residential history, socioeconomic characteristics of the parents, infections, exposure to radiation in utero or as a child, and parental smoking are some of the factors previously associated with childhood leukemia and such information, if available, can be included. Birth order is of interest because it has been implicated as a risk factor for leukemia and may be a marker of exposure to infectious agents, with later-born children presumed to be exposed more often and at earlier ages from their older siblings. Therefore, birth order could be used as a proxy to examine the postulated population mixing hypothesis and infectious etiology for childhood leukemia (Kinlen, 1988). According to this hypothesis, childhood leukemia is a rare response to common infection, which may be introduced to a previously isolated rural community by sudden in-migration and changes in the dynamics of infectious diseases. As stated earlier, the retrospective birth cohort study was judged by the committee to have high scientific merit but involves logistical and administrative barriers. A record-linkage-based case-control study that uses data on cancer registration and birth records to identify cases and controls and relevant information is an alternative to the retrospective birth cohort design. In a record-linkage-based case-control study, children diagnosed with cancer at age 0-14 years are identified from population-based cancer registries of states that have or have had a nuclear facility or are adjacent to such a facility. Cancer cases identified among children in the registry are linked to birth records within the respective state(s). Those born within the area of interest (e.g., 50 km around a nuclear facility) are eligible cases. One or more controls are randomly selected from birth records restricted to those born within the 50-km zone from the facilities, with matching to cases on year of birth at minimum, and if possible month of birth, race/ethnicity, and gender. The 50-km zone provides a wide range of potential exposures for controls but keeps controls in similar regional settings. Children diagnosed with cancers but who were born outside the study area could be excluded from the control group; however, the likelihood of them being selected randomly as controls is very small as indicated below. The record-linkage-based case-control study of pediatric cancers differs from the retrospective cohort in some important issues that enhance its feasibility by: 1.Restricting the linkages to within state instead of across states. Rather than considering (for example) all of the 3,000 childhood leukemia cases per year that are expected nationwide for linkage to birth registry information for all states with or proximal to nuclear facilities, cases would be identified from state cancer registries with or near facilities, and linkages would occur only within the respective states as opposed to between states. This should reduce considerably the number of birth records that need to be searched for each cancer case included. Also, as a consequence of restricting the cases to those born and diagnosed in the same state, the record-linkage-based case-control study focuses on the more residentially stable children (although arguably the children and their families may have moved within the state in which the child was born). 2.Limiting the number of cases and controls that would be followed to update residential history, or dropping the requirement. As a relatively small number of controls for each study case would be selected for analysis along with the cases (since many fewer study subjects would be involved than in the retrospective cohort study) it may potentially be more feasible to follow these forward and retrieve residential information than it would be to follow an entire birth cohort forward to look at changes in residence, in order to refine dose estimates. This effort still, however, could be substantial and may be worth doing only for a relatively small number of cases and controls in order to give estimates of overall rates of out-migration and loss to follow-up. Dropping the requirement of following the subjects forward in time via records, the overall efforts required to conduct the study are substantially reduced. As with the retrospective cohort design, cases as well as controls are required to be born within a fixed region (e.g., 50 km from a nuclear facility). For the record-linkage-based case-control design more selective targeting schemes could be considered, such as requiring the cases selected for study to be residents of a 50-km proximity zone at the time of diagnosis. It must be kept in mind, however, that as further restrictions for selecting eligible cases apply, the potential for loss of study power increases if large numbers of cases were excluded from consideration. Additionally, as the design does not rely on follow-up of the controls to establish if they also remained at the 50-km zone from birth to the time that the cases were diagnosed, the potential for selection bias increases and false relationships between case status and distance could appear if the probability of moving versus staying within the same region is inhomogeneous with respect to distance from nearest nuclear facility. Results from regions with high in- or out-migration of children would be less reliable than those from regions with less population mobility. The design could be extended as far back as registries with good quality data exist and birth years of cases and controls would co-extend with good practices of registry operation. A study that includes subjects that were born before the state’s cancer registration is of acceptable quality could appreciably increase the number of eligible cases at the older targeted ages, and it also could assess exposures in earlier years when the exposure levels were likely higher. Inclusion of these subjects can be achieved as follows: For cancer cases at each age X, the birth records for up to Y years before the beginning of good quality cancer registration could be used. For instance, if the year of good quality cancer registration data is 1996, the birth records from 1990, 1991, or 1992 could be used to include cancer cases and controls of ages 6 or older, 5 or older, 4 or older, respectively. While this approach might introduce slight bias as those who developed cancer at earlier ages would not be eligible, for all practical purposes the study could be regarded as unbiased on that respect. An advantage of either the record-linkage-based case-control approach or the retrospective cohort study is that certain relevant characteristics of the parents and infant are available on birth records and, depending on the year and state, would include: mother’s address; duration of residency at that address, parental age, race/ethnicity, educational level; and date of birth, gender, weight, and order of birth of the index child. Additional information on the birth certificate such as substance abuse by the mother (including smoking and alcohol) does exist in certain cases but will have varying reliability and completeness depending on the state (Spector et al., 2007). The above-mentioned data elements are included on the 2003 national standard certificate of live birth; however, the certificate was not implemented systematically. As described elsewhere, 2 states implemented use of the certificate in 2003, 7 additional states in 2004, and cumulatively 15 states used it in 2005 (Kirby and Salihu, 2006). Information on abnormal conditions of the infant such as Down’s syndrome and other congenital anomalies of the newborn can be used to exclude cases and controls from subanalysis. Regarding these issues, in a five-state pooled analysis study of parental age (available from birth records) and risk of childhood cancer (Johnson et al., 2009) which used the methodology described here, diagnoses went back to 1980 in Washington State, 1985 in New York State, 1988 in Minnesota and California and 1990 in Texas. The analysis from five states comprised approximately 30 percent of the U.S. pediatric population. Using probabilistic record linkage, the linkage success of cancer registry and birth records data within a state was 88 percent for leukemia cases age <5 years in California (Reynolds et al., 2002), 87 percent for hepatoblastoma cases age <5 years in New York (McLaughlin et al., 2006), and 82 percent for cancer cases age <15 years in Minnesota (Puumala et al., 2008). The information was not reported for Washington (Podvin et al., 2006) or Texas (Walker et al., 2007). Although the authors did not provide a breakdown of the possible reasons for unsuccessful linkage, these may include inmigration (children born elsewhere moved to the reference state and were diagnosed there), rather than flaws in the linking methodology. A 17-county study of childhood leukemia (age <15 years) in California demonstrated that a small percentage of cases (12 percent) were not born in the study area; approximately 5 percent were born in other counties in California and 7 percent outside of California (Ma et al., 2004). The recent study in Switzerland, a country where populations are likely less mobile than in the United States, demonstrated that 68 percent of pediatric cases had not moved between birth and diagnosis, 22 percent had moved once, 6 percent three times, and 4 percent three times or more. Although in-migration is expected in all states under study and appears to be somewhere between 10 and 20 percent for children 0-14 years, it is expected to be lower for children 0-5 years old (Ma et al., 2004), which is also the age range in which most leukemia cases are expected (peak for acute lympho-blastic leukemia is 2-4 years old). It may be possible to estimate in- and out-migration of subjects based on census data and to describe the characteristics of the cases who migrate based on cancer registry data such as age, year of diagnosis, and race; correction for selection bias may be possible if probabilities of exposure can be stratified by these same variables. Study controls in the record-linkage-based case-control design are randomly selected from each state’s birth registry. The matching ratios for the pooled analysis of the five states mentioned above differed by state from 1:1 to 1:10 (Johnson et al., 2009). A concern is that children identified by the birth registries as eligible controls may have been diagnosed with cancer in a different state. However, given the rarity of childhood cancers (about 4.8 per 100,000 children will be diagnosed by age 15 with leukemia or brain cancers, the two most common cancers in children), this issue should have essentially no effect on the power of a study, but might nevertheless have some unknown potential to introduce bias, since controls but not cases may have migrated from the state and such migration might reflect socioeco-nomic or other differences that affect childhood cancer risk. Feasibility of the record-linkage-based case-control study depends on availability and release criteria of the information on both birth and cancer registration information that may involve demanding Institutional Review Board (IRB)13 or equivalent body approvals. Release of the required information may not be possible in all states under investigation, or in rural areas within the states for reasons of subject protection or because linkage capabilities are not in place. For these reasons, it may not be possible to include all of the states of interest in the analysis. Part of the predicted feasibility and practicality of this study lies in the fact that it can be based on and expand on existing studies and ongoing efforts to link state cancer registry records with birth records, by partnering with the appropriate investigators. Such linkages are established statewide within Washington, New York, Minnesota, California, and Texas. Similar linkage analyses have been performed in metropolitan regions and surrounding counties of Seattle, Washington; Detroit, Michigan; and Atlanta, Georgia, as well as statewide in Utah (Mueller et al., 2009), to investigate pregnancy outcomes in female childhood and adolescent cancer survivors. The committee also considered the development of a new case-control study. To illustrate, a study of childhood cancer might begin with definition of a reference population of children less than 15 years old, living in the vicinity of nuclear facilities. Controls would be children of the same age and gender who lived in the same general area with the cases at the time the cases were diagnosed. Contact with children or families would be used to define residential history and therefore the study is not dependent on assumptions about continued nearby residence from birth until time of diagnosis. The challenges of selecting appropriate controls through random-digit dialling, school records, or friend controls and the emerging use of birth record controls are discussed in Section 4.3.4. It is important that controls be selected in a way that does not bias the basic comparisons that are the object of the study. In particular, controls must represent the distribution of distances from the nearest nuclear facility for the same population from which the cases are being drawn. Within a case-control study, investigators would usually choose the recent cases (for example, those diagnosed during the period 2005-2010) and appropriate controls and trace individuals for interviews in order to collect information on residential history and other risk factors and refine the exposure of the individuals. Tracing recent cases tends to be more successful than tracing past cases as the more recent cases would have less opportunity to move, would be easier to find, and are more likely to be alive. Children with cancer would be traced through the treating institution as identified from cancer registration files or other means and they and/or their parents contacted in order to obtain additional information regarding residential history and a list of known or putative risk factors for childhood cancer. If the identified cases who were children at diagnosis and are adults at the time of interview are those providing the information, their responses may differ from those of the parent, and many now-adults may not know answers to questions about childhood residential history or early life care. (Cancer registries may require that contact with the now-adult is established first to obtain permission to be a study subject and to allow parental contact.) Depending on the method selected for control identification, tracing for controls may also be required (see Section 4.3.5). Even when tracing is successful, collection of detailed information by interviews or by questionnaires will face issues of nonparticipation. As nonparticipation rates are often considered an indicator of the potential for selection bias, it is important that they are kept as low as possible; individuals (or parents) who refuse to participate in the study may differ in relevant ways from those who are willing to participate, and this may affect the study outcome. Controls often are more likely not to participate than cases, and participation rates of controls have declined in recent years, regardless of source (Bunin et al., 2007). One survey estimated the decline of population-based controls to be –1.86 percent per year (Morton et al., 2006). Low participation rates or differential participation rates between cases and controls can introduce bias, when willingness to participate is related to exposure and this tendency is stronger (or weaker) in cases than in controls (Hartge, 2006). Differences in the accuracy and detail of answers provided need to be minimized. Focus groups and pretests of questionnaires and procedures may help to establish a well-designed questionnaire for the specific study scope. To avoid bias associated with information given during an interview or when filling out a questionnaire, one useful approach is to not inform interviewers whether a specific subject is a case or a control; this can limit the bias that an interviewer might unconsciously inject into the information, though information on case or control status may often come out during the interview. In contrast, a patient (or proxy) cannot be kept in ignorance of his or her status, so an additional concern is “recall bias,” under which controls may have given less thought or pay less attention to past exposures (such as infections, medical imaging, and other) and underreport them, thus introducing a bias. For example, a mother whose child has died of leukemia may be more likely than the mother of a healthy living child to provide more complete and accurate information on past experiences such as x-ray exposures when the child was in utero (see Section A.4.6.2, Appendix A). This recall bias could artificially suggest a relation between x rays and leukemia. Moreover, the information that individuals give may be affected by unconscious biases; this is particularly true if a study has been widely publicized and subjects are aware of reported health effects and what exposures are suspected to cause these effects. A well-designed questionnaire may minimize these biases by carefully wording the questions, often requesting the same information by two questions phrased differently to identify inconsistencies and judge the reliability of the information, or simply by forcing the individual to think more carefully. Telephone interviewing may be a better approach than interviews in person, especially when questions touch on sensitive matters such as possible exposures during pregnancy. In a study of childhood leukemia the questionnaire is likely to contain details on lifestyle, socioeconomic status, residential history, occupational exposure of parents at the time of conception of the child and during pregnancy, medical radiation exposure during pregnancy and early childhood, infectious diseases during early childhood, contact with other children during first years of life, nursery care, birth order, and number of children in the family as well as questions specific to milk consumption to better estimate individual exposure. As most risk factors for leukemia are still unknown, it may be necessary to consider trade-offs between collecting a large amount of information per subject and the number and geographic source of subjects. Experience from previous studies in similar populations and areas often provides useful lessons learned. As shown in Section 4.2.1.6 a study which would have good power to detect 20 percent increases in cancer risk for a relatively rare exposure (RR = 1.2, assuming 2.5 percent of subjects are exposed in the calculations in Figure 4.3) would have to be extremely large (thousands of cases and at least as many controls). For rare cancers (such as childhood leukemia) this would involve decades of accrual in regions near sites; while much larger relative risks could be detected far more easily, the expectation is that 20 percent increases are extremely large relative to the cancer risks expected based on reported releases. For more common cancers, while the rates of case accrual are larger, the expectation is for even weaker dose-response relationships. Thus, the power of any feasible case-control study (one that could be completed in years rather than decades) is likely to be extremely low. For reasons primarily related to considerations of both statistical power and logistics, combined with the fact that only relatively recently diagnosed cases could be included and the potential for participation (and possible information) bias, a de novo case-control study and the associated efforts required to collect additional information on potentially confounding factors may not be justified over the record-linkage-based case-control approach. As discussed earlier in this section, it may be possible to partner with investigators who are already using linkages between cancer registration and birth records to perform the record-linkage-based case-control study. As these linkages exist in at least six states, representing more than 30 percent of the U.S. pediatric population, using existing data, if possible, would reduce substantially the overall efforts required to conduct the record-linkage-based case-control study. Several recent or ongoing case-control studies, cohort studies, and clinical trials could be useful in developing a new case-control study with contact of individuals or their proxies. The advantage of working with existing studies is that cancer cases and controls have already been identified, the initial contact has been established, and collected information related to the original study may be useful. Participants or their proxies can be recontacted and additional relevant information can be requested such as residential history and potential confounders. In certain instances it may be possible to find existing data about residential history passively (from old city directories, for example), without individual participant contact. Here, however, we assume that (as for most studies) individual exposure and covariate data are obtained directly from participants or their families. The requirement for direct contact would seem to require that the existing study contains recently diagnosed cases and that patients or families be contacted soon after diagnosis. This limits the number of existing studies that would be useful as partners. Most existing large studies are focused on adults, and often for populations with specific characteristics and outcomes to serve the specific research focus of the study. A few such examples are the Women’s Health Initiative, a study of more than 160,000 generally healthy postmenopausal women, designed to test—among other issues—the effects of postmenopausal hormone therapy on breast and colorectal cancer (Hays et al., 2003), and the Nurses’ Health Study, a study of about 238,000 female nurses, focused primarily on cancer prevention (Willett et al., 1987). For rare cancers such as pediatric cancers, investigators have realized that individual large cohort studies are unable to examine the effect of different exposures on the disease due to inadequate sample size. For that reason, multiple large children’s cohorts have joined to establish national or international consortia such as the Pediatric Brain Tumor Consortium and the International Childhood Cancer Cohort Consortium. Even if existing studies include the age group and cancer outcome of interest, the biggest issue is that, since only a relatively small fraction of the U.S. population overall lives quite near a nuclear facility (about 0.3 percent within 8 km and 15 percent within 50 km in 2010; see Tables 1.3 and 1.4 in Chapter 1), existing studies probably do not cover enough persons living within the 0-50-km zone to provide statistical power for the study of the relation between residential history and/or individually estimated exposures and cancer occurrence. The possibility of using an existing study to build a contact-based case-control study was not considered further, since no known studies that would meet the necessary criteria were identified. Of the several studies considered, two epidemiologic study designs were judged by the committee as suitable to have scientific merit and address the nonscientific issues that they must deal with for assessing cancer risks in populations near nuclear facilities: the ecologic and record-linkage-based case-control studies. A summary of the strengths and limitations of the recommended studies is presented here. Description The study design investigates incidence and mortality rates for all common cancers identified at the census tract within which cases reside at the time of diagnosis or death from cancer, respectively. The study is restricted to census tracts within a fixed distance (perhaps 50 km) of a facility which represents a range of potential exposures from the highest to essentially no exposure. Cancer rates among census tracts are compared by average estimated levels of exposure. The question such a study can answer Are observed cancer incidence and/or mortality rates higher in census tracts with higher estimated exposures (as estimated from reported releases from the nuclear facility)? Feasibility14 depends on a.Availability and release of aggregated cancer registry and mortality information at the census-tract level, according to age, gender, race/ethnicity, and cancer site. b.Availability of population structure and size (also by age, gender, race/ethnicity) data from the U.S. census, with interpolation for noncensus years. Strengths a.Has the ability to look at all potentially radiosensitive types of cancers and for all age groups. b.Examines both incidence and mortality, which provide complementary data and can be mutually supportive. c.Can examine past outcomes and therefore can examine risks at times when releases were higher and more likely to cause cancer. d.Only cancer registries and/or vital statistics offices of those states that have or have had a nuclear facility or which contain populations within the study distance of a nuclear facility need to be contacted. e.Provides results relatively quickly as information comes mostly from existing databases. f.No issues related to control selection appropriateness or feasibility. g.Does not rely on recruitment of study participants. h.IRB or equivalent body approvals for cancer incidence and mortality data will possibly be needed, but procedures are likely to be undemanding (possible exceptions are procedures for data release from rural areas where only a few cases reside within a census tract). Limitations a.Subject to ecologic fallacy and has limited ability to conclusively establish or refute a relationship between radiation and cancer because exposure information on actual cancer cases is not obtained; might be subject to biases that cannot be taken into account. Is considered hypothesis generating. b.Study type has been criticized. It may be viewed as an easy, quick, and least expensive study, bound to give inconclusive results because:
Can only examine associations based on residence at diagnosis or death rather than place of birth or place of relevant exposure. Associations based on place of death may only partially reflect past exposures due to population mobility. d.Can only estimate average in- and out-migration rates, with no information on the residential history of actual cancer cases. Description Children diagnosed with cancer (in the period of reliable cancer registration) in states that have or have had a nuclear facility or are within a fixed distance (for example, 50 km) of a nuclear facility are linked to the birth records of the respective states to identify those children that developed cancer and were born within a fixed distance from the facility (for example 50 km). Controls are children identified from birth records to be born in the same general study area as cases and matched at minimum to cases on year of birth (birth month and gender where possible). The question such a study can answer Among children born within 50 km of a nuclear facility, are pediatric cancers associated with higher exposure at maternal residence at time of birth? Feasibility depends on a.Availability of maternal residence at the time of delivery in the birth records. b.Within-state linkage capability of cancer registration with records kept in vital statistics offices that will provide information on births (and possibly deaths) in the areas around the facilities. c.Availability and release of linked data at the individual level. d.Accrual of enough childhood cases during the times in which cancer registries are of reasonable quality to have power to detect disease patterns related to estimated exposure levels. e.Ability to obtain birth record information on all births in the relevant risk sets (e.g., all those born within 50 km of the nuclear facility in each of the relevant birth years) in order to define an unbiased set of geographic controls. Strengths a.Provides individual risk estimates rather than estimates based on geographic units. b.Examines associations relevant to early life exposures (birth place) which can be considered more relevant than those later in life as would be captured in a study based on place of residence at time of cancer diagnosis or death from cancer and the equivalent for the unexposed. c.Can be considered an objective study as it does not rely on contact of individuals or interviews and therefore is not subject to selection or possible information bias related with subject participation and collection of information on risk factors. d.Does not need to be restricted to very recent cases, as cases and controls are not traced to be interviewed. e.Provides results relatively quickly as information comes from existing databases and requires linkage only between cancer and birth registration data. f.Information on certain relevant covariates is available in the birth certificates and can be adjusted for. g.Because the study is focused on children, uncertainties sourcing from population mobility or lifestyle choices are less of a concern. h.In-migration of cancer cases (but not controls) can be estimated. Limitations a.Restricted to a specific age group and few cancer types (i.e., childhood cancers). Hence, it may not address many of the concerns of the public stakeholders. b.Restricted to recent cases, therefore
Cannot estimate the frequency of, or the altered exposures and effect estimates due to, out-of-state migration of cases or any migration of controls. d.Linkage of birth and cancer registry records may not be possible (or permitted) in some states. e.IRB or equivalent body approvals for data release of birth and cancer registration will be required. The recommended studies are complementary in that each addresses different aspects of cancer risks:
The recommended studies are mutually independent, and could be carried out individually or together. The decision on which of the recommended studies to carry out and their order of execution involves a host of policy and other considerations that are beyond the scope of this Phase 1 project. These include, for example, considerations such as the following:
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