Cases and Controls
A case-control study compares two groups of people: those with the cancer under study (cases) and those who do not have the cancer (controls). Researchers compare the genetic, environmental, lifestyle, and medical histories of the people in the two groups to identify factors associated with cancer.
Selected examples of DCEG case-control studies:
AsiaLymph , an international hospital-based case-control study of lymphoma among Chinese in Eastern Asia to replicate and extend recent and novel observations made in studies of White populations with distinctly different patterns of environmental and occupational risk factors and genetic loci.
African Esophageal Cancer Consortium (AfrECC) facilitates collaborations to coordinate etiologic and molecular studies of esophageal squamous cell carcinoma in East Africa.
Breast, Ovary and Endometrial Cancer Studies in Poland
- Ovarian and Endometrial Cancer Case-Control Study in Poland was conducted among female residents of Warsaw and Lodz (Poland) between 2001 and 2003. Current projects include methylation profiling, tumor gene sequencing, microsatellite instability analysis, and immunohistochemistry to study the etiologic heterogeneity of endometrial and ovarian cancers.
Case-control Studies of Renal Cell Cancer
- Renal Cell Cancer among White and African American Adults in the United States , conducted in the metropolitan areas of Detroit and Chicago in collaboration with Wayne State University and the University of Illinois at Chicago. The aims of this study are to evaluate risk factors for renal cell cancer and examine why rates of this disease are higher among U.S. Black adults than White adults.
- Renal Cell Cancer in Eastern Europe , conducted from 1999 to 2003 in collaboration with the International Agency for Research on Cancer to evaluate kidney cancer risks in relation to occupational and other environmental and lifestyle exposures in six centers across Eastern Europe. Factors being evaluated include occupational exposures, lifestyle factors, medical conditions, markers of genetic susceptibility, and tumor molecular characteristics.
The DETECT Study – Discovery and Evaluation of Testing for Endometrial Cancer in Tampons , a partnership with the University of Alabama Birmingham to evaluate the acceptability and feasibility of self-sampling with vaginal tampons for endometrial cancer detection in a racially-diverse population of women undergoing hysterectomy.
Environment And Genetics in Lung cancer Etiology (EAGLE) is a large population-based case-control study designed and conducted to investigate the genetic and environmental determinants of lung cancer and smoking persistence using an integrative approach that allows combined analysis of genetic, environmental, clinical, and behavioral data.
Epidemiology of Burkitt Lymphoma in East African Children and Minors (EMBLEM) , a large, multidisciplinary epidemiological effort designed to evaluate environmental and host factors associated with childhood Burkitt lymphoma (BL) in sub-Saharan Africa.
Nasopharyngeal Case-Control Study , conducted in Taiwan between 1991-1994 and 2010-2014, examines the role of viral, environmental, and genetic factors associated with the development of nasopharyngeal carcinoma (NPC). Factors investigated include Epstein-Barr virus, diet, smoking, occupation, HLA, and other genetic polymorphisms.
NCI-SEER Non-Hodgkin Lymphoma (NHL) Case-Control Study , a multi-center, population-based study of 1,321 NHL cases and 1,057 controls that includes detailed interview data, biospecimens, and environmental samples.
New England Bladder Cancer Study , a population-based, case-control study of bladder cancer in New Hampshire, Vermont, and Maine, is designed to explain the reasons for the persistent excess of rates of bladder cancer in the northern New England area. Investigators collected data on 2,600 participants via personal interviews, biological samples (blood, buccal cells, urine, toenails, and tumor tissue), as well as drinking water samples.
Testicular Cancer among Military Servicemen: the STEED Study , a case-control study of testicular cancer among military servicemen. The project includes obtaining biosamples and questionnaire data from all participants. Pre-diagnostic serum samples are available from the approximately 1,100 cases and 1,100 controls enrolled in the study.
Transplant Cancer Match Study , a collaborative effort with the Health Resources and Services Administration, which oversees the U.S. solid organ transplant network. Data from multiple state and regional cancer registries are linked with the U.S. registry of transplant recipients, to cover more than 50% of the U.S. transplant population.
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- v.8(57); 2017 Nov 14
A case-control study on risk factors of breast cancer in Han Chinese women
1 Department of Breast Surgery, The Second Hospital of Shandong University, Jinan, Shandong, 250033, China
2 Department of Breast Surgery, Affiliated Tumor Hospital of Zhengzhou University, Zhengzhou, Henan, 450008, China
3 Department of Breast Surgery, Shanxi Cancer Hospital, Taiyuan, Shanxi, 030013, China
4 Department of Breast Surgery, The First Hospital of Jilin University, Changchun, Jilin, 130021,China
5 Breast Center, The Fourth Hospital of Hebei Medical University, Shijiazhuang, Hebei, 050011, China
6 Department of Breast Surgery, Tianjin Medical University Cancer Institute and Hospital, Tianjin, 300060, China
7 Department of Thyroid and Breast Surgery, The First Affiliated Hospital of Binzhou Medical University, Binzhou, Shandong, 256603,China
8 Department of Breast Surgery, Cancer Hospital, Chinese Academy of Medical Sciences, Beijing, 100021, China
9 Department of General Surgery, Linyi People’s Hospital, Linyi, Shandong, 276003, China
10 Breast Disease Center, Peking University People's Hospital, Beijing, 100044, China
11 Department of General Surgery, Beijing Chaoyang Hospital, Beijing, 100043, China
12 Breast Disease Center, Peking University First Hospital, Beijing, 100034, China
13 Breast Center, Qingdao University Affiliated Hospital, Qingdao, Shandong, 266003, China
14 Department of Breast and Thyroid Surgery, Weifang Traditional Chinese Hospital, Weifang, Shandong, 261041, China
15 Department of Breast Surgery, The Second Affiliated Hospital of Qingdao Medical College, Qingdao Central Hospital, Qingdao, Shandong, 266042, China
16 Department of General Surgery, The Second Affiliated Hospital of Harbin Medical University, Harbin, Heilongjiang, 150001, China
17 Department of Breast Surgery, The First Affiliated Hospital of China Medical University, Shenyang, Liaoning, 110001, China
18 Department of General Surgery, Nanjing Medical University Affiliated Cancer Hospital, Cancer Institute of Jiangsu Province, Nanjing, Jiangsu, 210009, China
19 Department of Breast and Thyroid Surgery, Zibo Central Hospital, Zibo, Shandong, 255036, China
20 Department of Breast Surgery, Yantai Yuhuangding Hospital, Yantai, Shandong, 264000, China
21 Breast Cancer Center, Shandong Cancer Hospital, Jinan, Shandong, 250117, China
Yu-juan xiang, qiang zhang, zhong-bing ma, de-zong gao, chun-miao ye, yong-jiu wang, wen-zhong zhou, zhi-gang yu, associated data.
This study aimed to investigate risk factors associated with breast cancer among Han Chinese women in northern and eastern China. A matched case-control study involving 1489 patients with breast cancer and 1489 controls was conducted across 21 hospitals in 11 provinces in China, from April 2012 to April 2013. We developed a structured questionnaire to record information from face-to-face interviews with participants. Student’s t-tests, Pearson’s chi-square tests, and univariate and multivariate conditional logistic regression analyses were used to identify variables with significant differences between the case and control groups. Ten variables were identified (P < 0.05): location, economic status, waist-to-hip ratio, menopause, family history of breast cancer, present life satisfaction, sleep satisfaction, milk products, behavior prevention scores, and awareness of breast cancer. We identified a comprehensive range of factors related to breast cancer, among which several manageable factors may contribute to breast cancer prevention. Further prospective studies concerning psychological interventions, sleep regulation, health guidance, and physical exercise are required. A screening model for high-risk populations should be put on the agenda.
Breast cancer is the most common type of cancer worldwide; the incidence is continuing to rise, and it is the leading cause of cancer-related death among women [ 1 , 2 ]. World Health Organization (WHO) statistics show there were 1.67 million new breast cancer cases diagnosed in 2012, accounting for 25% of all cancers diagnosed that year [ 3 ]. Reports in China indicate the annual increase in the incidence of breast cancer has doubled or tripled over the past two decades, making it the leading cancer among women [ 4 – 6 ].
Characteristics of established risk factors for breast cancer may vary among countries. Better understanding the characteristics of local risk factors may inform more effective breast cancer prevention strategies [ 7 ]. When risk factors are well understood, healthcare providers are able to supply women with more accurate information regarding their individual risk of developing breast cancer [ 8 ]. Cancer risk assessment has emerged as an important component of cancer risk counseling [ 9 – 11 ].
Worldwide, numerous studies have sought understand the risk factors for breast cancer. However, there has been no consensus because of differences in sample sizes, races that comprised study populations, and local customs. Most epidemiological studies have evaluated risk factors for breast cancer based on large sample sizes in Western populations. However, these risk factors are not based on Chinese women and cannot be directly applied in China, because risk factors may differ across different populations [ 12 – 14 ]. In China, breast cancer risk factors have received considerable attention. Several case-control studies have been conducted to screen potential risk factors in various local areas; however, most studies included small sample sizes. Currently, national monitoring data on risk factors among the Chinese general population are limited. This study aimed to investigate risk factors for breast cancer among Han Chinese women. Risk factors determined in our study will help to identify Chinese women who have an increased risk of breast cancer, and support effective early detection and disease prevention interventions.
Figure Figure1 1 shows the study implementation process. We initially recruited 1613 pairs of 1:1 matched cases and controls. Of these women, 1489 pairs were eligible for enrollment in the study, as 124 pairs were excluded after logical checks (16 with benign diseases in the case group, 46 with malignant diseases in the control group, 10 with non-Han ethnicity, seven with non-matched age, 13 with duplicate enrollment, 22 with relapse diseases, and 18 with incomplete information). We found that 1120 participants (37.61%) had full understanding of the questionnaire, 1450 (48.69%) mostly understood the questionnaire, 224 (7.52%) had partial understanding, and eight (0.27%) did not understand the questionnaire. In total, 1714 women (57.56%) fully cooperated with the investigation, 1035 women (34.75%) were basically cooperative, and 41 women (1.37%) did not cooperate.
Among the 1489 patients with breast cancer, there were 1128 cases with invasive ductal carcinoma (accounting for 75.8% of the study population), 127 (8.5%) with intraductal carcinoma, 24 (1.6%) with invasive lobular carcinoma, and 194 (10.7%) with other types of cancer (including mucinous breast carcinoma, neuroendocrine carcinoma, comedocarcinoma and medullary carcinoma). Luminal A type, luminal B type, HER-2 type, and triple negative types accounted for 10.7% (n=159), 49.9% (n=743), 8% (n=119), and 8.5% (n=126) of cases, respectively. In addition, 322 cases were estrogen receptor negative (21.63%), 1018 were estrogen receptor positive (68.37%), 149 had lost estrogen receptor status (10.01%), 417 were progesterone receptor negative (28.01%), 951 were progesterone receptor positive (63.09%), and 121 had lost progesterone receptor status (8.13%).
Demographic characteristics for the case and control groups are shown in Table Table1. 1 . There were statistically significant differences between the two groups. Of the 1489 cases, 92 (6.2%) were aged 25–34 years, 451 (30.3%) were aged 35–44 years, 588 (39.5%) were aged 45–54 years, 315 (21.2%) were aged 55–64 years, and 43 (2.9%) were aged over 65 years. Patients aged over 45 years accounted for 63.5% of all cases, and there were no significant differences between the two groups (χ 2 =5.172, P=0.222). However, there were differences in education levels (χ 2 =65.333, P<0.001), location (χ 2 =60.900, P<0.001), family average revenue (χ 2 =98.827, P<0.001), economic status (χ 2 =104.593, P<0.001), social status (χ 2 =77.895, P<0.001), and awareness of breast cancer (χ 2 =20.585, P<0.001) between the two groups.
There were no differences between the case and control groups in age at menarche (7−11 years, 74.0% vs. 73.5%), menstrual pattern (irregular, 6.4% vs. 5.7%), and marital status (never married, 6.4% vs. 4.9%). However, there were significant differences between the two groups in postmenopausal status (χ 2 =8.244, P=0.004) and number of births (χ 2 =36.026, P<0.001). No significant differences were found for breastfeeding, number of miscarriages, and use of oral contraceptives (Table (Table2 2 ).
Table Table3 3 shows the characteristics of chronic diseases in the case and control groups. There were statistically significant differences in hypertension (χ 2 =4.625, P=0.032), benign tumor of the breast (χ 2 =26.957, P<0.001), galactophore hyperplasia (χ 2 =14.520, P<0.001), nipple discharge (χ 2 =5.849, P=0.016), and family history of breast cancer (χ 2 =13.168, P<0.001). Variables not associated with significant differences were diabetes mellitus (4.0% vs. 3.4%), inverted nipple (1.3% vs. 0.8%), and multiple breasts (1.3% vs. 2.0%).
There were significant differences between the case and control groups in cigarette smoking (χ 2 =5.862, P=0.015), tea drinking (χ 2 =5.250, P=0.022), and sleep satisfaction (χ 2 =15.892, P<0.001), but no differences in alcohol drinking (1.0% vs. 0.8%), coffee drinking (4.8% vs. 5.6%), and physical activity (71.6% vs. 74.1%) (Table (Table4). 4 ). Characteristics of dietary habits in the case and control group are shown in Supplementary Table 2 .
Body size measures for cases and controls are shown in Table Table5. 5 . The mean height (± standard deviation) of cases was 160.03 cm (± 4.78 cm) and that of controls was 160.38 cm (± 4.31 cm). Body mass index (BMI) was higher in cases compared with controls (t=2.599, P=0.009). There were statistically significant differences in waist circumference (t=5.106, P=0.009), hip circumference (t=2.176, P=0.030), and waist-to-hip ratio (WHR) (t=2.704, P=0.007) between the case and control groups.
Table Table6 6 shows blood parameters for the case and control groups. No significant differences between the groups were observed in adiponectin, including total adiponectin (t=−1.393, P=0.164) and high-molecular-weight (HMW) adiponectin (t=−0.840, P=0.401). In addition, there were no significant differences in triglyceride (t=1.580, P=0.144) and total cholesterol (t=0.093, P=0.926) levels.
All variables included in the questionnaire were analyzed using matched conditioned logistic regression analysis (Table (Table7). 7 ). Significant differences (α=0.05) between the case and control groups were observed for: location, education, economic status, social status, hypertension, family history of breast cancer, menopause, BMI, WHR, sleep satisfaction, present life satisfaction, cigarette smoking, bean products, vegetables , milk products, behavior prevention scores, and awareness of breast cancer. Multivariate Cox regression models were performed to analyze risk factors for breast cancer (α=0.10). Nine factors were significantly related to breast cancer, for which the odds ratios (OR) and 95% confidence intervals (CI) were: location, 1.269 (0.984–1.638, P=0.067); economic status, 1.237 (1.019–1.501, P=0.032); family history of breast cancer, 2.418 (1.361–4.294, P=0.003); menopause, 1.982 (1.360–2.888, P<0.001); WHR, 1.329 (0.983–1.797, P=0.065); sleep satisfaction, 1.412 (1.140–1.749, P=0.002); present life satisfaction, 1.852 (1.436–2.390, P<0.001); milk products, 0.813 (0.716–0.923, P=0.001); behavior prevention scores, 0.685 (0.517–0.907, P=0.008); and awareness of breast cancer, 0.675 (0.520–0.876, P=0.003).
-, no data; NA, not available, there were strong correlations between these factors and other factors, and NA means that it was not included in the multivariate analysis; CI, confidence interval; BMI, body mass index; WHR, waist-to-hip ratio.
Multiplicative model interaction was assessed with a cross-product interaction term in our multivariate logistic regression model. Two-factor interaction analyses were conducted among statistically significant variables selected by the multivariate analysis. Positive interactions (at α=0.05) were observed for: family history and present life satisfaction; WHR and present life satisfaction; and WHR and sleep satisfaction (Table (Table7). 7 ). It is important to note that the interaction obtained through the logistic regression analysis represents a multiplicative model. For example, the interaction between family history and present life satisfaction indicates that for females with a family history of breast cancer, those with poorer life satisfaction have an increased breast cancer risk.
Development of breast cancer is a complicated and continuous progress, characterized by multi-step, multi-factor, and environment-gene interactions in origin. Although many studies on breast cancer development have been conducted, reported results varied widely. This may be related to disparities in study designs, geographical features, and lifestyle and healthcare factors. It is important to investigate and clarify risk factors for breast cancer, especially manageable factors, with which better prevention strategies could be formulated.
We described a case-control study involving 2978 Chinese Han women. In total, 75.8% of breast cancer cases were diagnosed as invasive ductal carcinoma, which is consistent with national and international reports. In China, invasive ductal carcinoma accounts for about 70% of all female breast cancers, whereas other tumor types (e.g., invasive lobular carcinoma) account for no more than 5% [ 15 – 18 ]. In our study, 50% of breast cancer cases were luminal B type, which is a much higher rate than in previous reports (11–23%). This disparity may be attributable to the new classification standard published by the St Gallen International Expert Consensus [ 19 ], which included both the progesterone receptor positive range (20%) and ki67 cutoff value (14%) for classification. According to this classification standard, some cases originally recognized as luminal A type were reclassified as luminal B type.
Our study (Figure (Figure2) 2 ) showed that the peak incidence of breast cancer was around age 45–55 years in both rural and urban areas. This is about 10 years earlier than in American and other Western countries (age 65 years). Compared with our previous study [ 20 ], that found bimodal patterns of incidence (one at 55–60 years and another at 60–65 years), no such patterns were observed. Previous Chinese studies reported obvious bimodal patterns of age-specific incidence, with the incidence of premenopausal breast cancer reported to be much higher than the postmenopausal incidence. However, this pattern changed over the past several years. For example, in the Shanghai Female Study [ 21 ] involving females aged 35–80 years, the age-specific incidence of breast cancer presented a gradual upward trend from 1973. Two age peaks were revealed before 2002 (especially 1998–2002), whereas a gradual shift toward a unimodal peak was observed from 2003–2007, which is consistent with our study.
Previous studies demonstrated a genetic susceptibility to breast cancer. Females with a family history of breast cancer, especially among first-degree relatives, were more likely to develop breast cancer. Moreover, the risk was further increased in cases where more than one breast cancer case had been diagnosed among first-degree relatives [ 22 , 23 ]. In our study, family history, first-degree relative family history, and second-degree relative family history were researched, and multivariate logistic regression and OR assessment were performed. We found that a family history of breast cancer doubled the risk of developing the disease (OR=2.418), which showed a similar trend to our previous study (OR=7.08) [ 24 ] and another Western report [ 23 ].
Obesity is another factor that contributes to the increasing incidence of breast cancer [ 25 – 27 ]. The incidence of overweight and obesity among female adults increased from 29.8% in 1983 to 38.0% in 2013 [ 28 ]. Currently, BMI and WHR are the most common measures for defining obesity and investigating associations between obesity and breast cancer. Compared with BMI, WHR may provide a better mean for evaluating central obesity, which is more common in China. Several studies have shown that high WHR is related to increased breast cancer risk [ 29 , 30 ]. In our study, both high BMI and WHR were correlated with increased risk of breast cancer (OR 1.010 and 1.115, respectively) in the univariate logistic regression analysis, but only high WHR remained after the multivariate logistic regression analysis (OR 1.329). This is consistent with results reported by Ali Montazeri [ 31 ] and Pathak [ 32 ]. However, the mechanisms by which overweight and obesity influence breast cancer development have not yet been elucidated. It has been proposed that high BMI is connected to increased insulin and insulin-like growth factors, which in turn contribute to the elevated risk of breast cancer. Arendt et al. [ 33 ] showed that a micro-inflammatory state, increased estrogen levels, and decreased insulin sensitivity secondary to obesity were potential links between obesity and breast cancer. A reasonable diet, physical exercise, medication, and even surgery may facilitate weight control, which may reduce breast cancer risk. Future prospective studies are needed o determine whether such methods would work.
A dietary pattern that includes a high-fat component, soy, dairy products, meat, fruits, and vegetables is supposed to affect breast cancer development and progress, although no consistent conclusions have been reached [ 34 – 36 ]. In our univariate logistic regression analysis, soy and dairy products were related to a reduced risk of breast cancer, with dairy products remaining after the multivariate logistic regression analysis. This is consistent with studies among females in Hong Kong [ 37 ]. However, a meta-analysis by Dong et al. [ 38 ] revealed no associations between dairy products and breast cancer risk. This disparity may be partly explained by regional variations in eating habits.
Psychological status should not be overlooked as a potential factor related to breast cancer development [ 39 , 40 ]. Many studies demonstrated that negative life events, depression, anxiety, irritability, and unhealthy psychological factors contributed to the development of system secondary to emotional stress [ 41 , 42 ]. In our study 12 items were used to assess overall life satisfaction and six items to assess current life satisfaction. High scores indicated low satisfaction or dissatisfaction, whereas low scores indicated high satisfaction. We found that low current life satisfaction was associated with an increased risk of breast cancer (OR=1.852), suggesting that psychological interventions should be considered in breast cancer prevention.
Previous studies showed that poor sleep quality (reported prevalence of 5–40%), was related to elevated risk of a variety of tumors [ 43 – 45 ]. In our study, insomnia, early awakening, sleeping late, and subjective sleep quality were correlated with breast cancer development in the univariate logistic regression analysis. The multivariate logistic regression analysis showed poor sleep quality was associated with increased risk of breast cancer (OR=1.412), which is consistent with some previous reports [ 46 ]. Given current epidemiological evidence, there is no agreement about the association between sleep quality and breast cancer, and the potential mechanism needs to be further studied.
We also investigated awareness of and knowledge about breast cancer-related symptoms and risk factors. Only 72.8% of participants knew breast cancer was a common cancer among females; 83.3% reported low awareness, and only 16.7% had high awareness. About 52.7% of women recognized a lump as a clinical manifestation of breast cancer, although only about 30.0% recognized other breast cancer-related symptoms such as breast discomfort, enlarged lymph nodes, nipple inversion, and nipple discharge. In addition, 63.3% knew that family history of breast cancer and long-term use of estrogen-like medicines were risk factors for breast cancer. The rates of awareness of other risk factors were below 30%. Correlation analysis suggested that high awareness was a protective factor for breast cancer, highlighting the importance and necessity of targeted publicity and education programs.
Based on previous findings that obesity may be related to increased breast cancer risk and poorer outcomes, we explored the association between adipokines and breast cancer. Adiponectin is considered the key link between obesity and breast cancer [ 47 ], especially postmenopausal breast cancer, although current studies have reported mixed conclusions [ 48 – 50 ]. In our study, both total adiponectin and HMW adiponectin serum levels were tested with the enzyme-linked immunosorbent assay (ELISA) method. When analyzed as continuous numeric variables, no associations were observed. However, when distinguished by a cut-off value on the receiver operating characteristic curve, a high HMW adiponectin level was correlated with reduced breast cancer risk. This conclusion was valid among postmenopausal women. No association between total adiponectin level and breast cancer risk was observed, which is consistent with previous studies [ 51 , 52 ]. Thus, the serum HMW adiponectin level was more likely to impact breast cancer development than the total adiponectin level.
Our study was a retrospective case-control study. As women self-reported their parity, breastfeeding, disease, and alcohol use histories, our findings may be subject to recall bias. To minimize recall bias, several similar questions were asked in different sections of the questionnaire. A 1:1 matched case-control design (by age and hospital) was used to control for possible confounders, and all interviewers were required to complete standardized training. In future, we aim to validate the risk and protective factors identified in this study using a case-cohort study.
We identified a comprehensive range of factors related to breast cancer. Among these there were several manageable factors that may contribute to breast cancer prevention. Future prospective studies are needed that consider psychological interventions, sleep regulation, health guidance, and physical exercise. In addition, a screening model for high-risk populations should be put on the agenda.
MATERIALS AND METHODS
We conducted a multi-center, hospital-based, case-control study of breast cancer among women in northern and eastern China. This study was funded by the Ministry of Health of the People’s Republic of China, and took place in 21 hospitals located in 11 provinces, from April 2012 to April 2013.
The target population was female outpatients with breast cancer aged 25–70 years in 21 hospitals. Cases and controls were matched (1:1) on age (± 3 years), diagnosis hospital (same hospital), and timing of examination (within 2 months). Inclusion criteria for breast cancer cases were: (1) newly diagnosed and histologically confirmed breast cancer; (2) Han ethnic group; and (3) females aged 25–70 years. Exclusion criteria for patients with breast cancer were: recurrent or metastatic breast cancer, complication of other malignant tumors by clinical or pathological diagnosis, and <25 or >70 years of age. Inclusion criteria for the control group were: (1) negative physical examination results; (2) negative ultrasound scans of breast and/or mammographic screening results; (3) no evidence of cancer or history of cancer; and (4) Han ethnic group. Patients who had a neoplastic disease at any other site, or history of cancer or other major chronic disease were excluded from the study. Data collection strictly adhered to the inclusion and exclusion criteria. After excluding those with inadequate information or missing data, 1489 case-control pairs were involved in this study.
We developed a self-designed structured questionnaire to record information obtained from participants during face-to-face interviews. The interview questionnaire was based on: published articles; the Gail, Claus, and international models; and discussions with experts in breast surgery, epidemiology, statistics, nutrition, and molecular biology. To minimize recall bias, several similar questions were asked in different sections of the questionnaire. A preliminary investigation was performed to assess the practicality and effectiveness of the survey. After repeated revisions, the final interviewer-administered questionnaire comprised seven parts. (1) Demographic characteristics and female physiological and reproductive factors (e.g., age, age at menarche, age at menopause, number of miscarriages, breastfeeding, dysmenorrhea, menopausal status). (2) Chronic diseases and family history (e.g., benign breast disease diabetes mellitus, hypertension, and family history of breast cancer—first- and second-degree relatives). (3) Lifestyle habits, including smoking (including passive smoking), alcohol intake, and dietary habits. (4) Medication and chemical exposure history (including hair dyes, antidiabetic agents). (5) Breast cancer-related knowledge (risk factors for breast cancer, early signs and symptoms of breast cancer). (6) Medical records, specifically, information gathered from the clinical breast examination (including results from visual examination, palpation, and related diagnostic tests; histological and immunohistochemical diagnoses of breast cancer patients were also collected). (7) Physical measurements (height, weight, BMI, hip and waist circumference, WHR, blood pressure, blood glucose, triglyceride, and total cholesterol).
For each participant, a 4-ml non-fasting blood sample was collected using an EDTA vacutainer. After sedimentation, each blood sample was stored vertically in a freezer at −80°C. Total and HMW adiponectin levels were assayed from plasma using human total adiponectin and HMW adiponectin quantitative ELISA kits, respectively (RD systems, SRP300, SHWAD0). All analyses were performed at the Central Research Laboratory, the Second Hospital of Shandong University. Testing of fasting plasma glucose, triglyceride, and total cholesterol were performed by the collaborating hospitals’ clinical laboratories.
Interviewers were medical professionals and medical post-graduates. All interviewer candidates were required to complete standardized training and were certified to conduct independent surveys. To minimize recall bias, several similar questions were asked in different sections of the questionnaire; for example, we used date of birth and age (years) to express actual age, years of schooling and highest degree to express education level, number of pregnancies = number of births + number of abortions, number of children = number of boys + number of girls. Solutions to contradictions are shown in Supplementary Table 1 . The questionnaires and forms were coded twice, and were double-entered by different clerks. Inconsistent records were manually checked and corrected. Computer programs were used to check the logic and reasonable range of responses throughout the questionnaire to identify contradictory responses.
All procedures performed involving human participants were in accordance with the ethical standards of the Second Hospital of Shandong University Research Committee. Written informed consent was obtained from all participants by investigators as part of the interview.
The database was established using Epidata 3.1 software (Epidata Association, Odense, Denmark). Frequencies and percentages were calculated for variables such as demographic characteristics, physiological and reproductive factors, chronic diseases and family history, lifestyle habits, medication and chemical exposure history, breast cancer-related knowledge, medical records, and physical measurements. We used Student’s t-tests and Pearson’s chi-square tests for the univariate analysis, and found 17 variables had significant differences (location, education, economic status, social status, hypertension, family history of breast cancer, menopause, BMI, WHR, sleep satisfaction, present life satisfaction, cigarette smoking, bean products, vegetable, milk products, behavior prevention scores, and awareness of breast cancer). Multivariate conditional logistic regression analyses were used to stratify independent variables with ORs and 95% CIs. All data were analyzed using SPSS version 16.0 (SPSS Inc., Chicago, IL, USA). A two-sided P-value <0.05 was considered to be statistically significant.
SUPPLEMENTARY MATERIAL TABLES
Acknowledgments and funding.
This research was primarily granted funding from the Minister-affiliated hospital key project of the Ministry of Health of the People’s Republic of China (establishment and improvement of high-risk populations screening and evaluation system for breast cancer), and the Key Project of the Natural Science Foundation of Shandong Province (plasma of high molecular weight adiponectin and single nucleotide polymorphisms and risk assessment of breast cancer, ZR2014HZ004). We would like to thank all participants involved in the study for their cooperation.
CONFLICTS OF INTEREST
The authors declare no competing financial interests.
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A case-control study of breast cancer risk factors in 7,663 women in Malaysia
- 1 Department of Applied Mathematics, Faculty of Engineering, University of Nottingham Malaysia Campus, Semenyih, Selangor, Malaysia.
- 2 Cancer Research Malaysia, Subang Jaya, Selangor, Malaysia.
- 3 Department of Surgery, Faculty of Medicine, University of Malaya, Kuala Lumpur, Malaysia.
- 4 Biomedical Imaging Department, Faculty of Medicine, University of Malaya, Kuala Lumpur, Malaysia.
- 5 Sime Darby Medical Centre, Subang Jaya, Selangor, Malaysia.
- 6 Jeffrey Cheah School of Medicine and Health Sciences, Monash University Malaysia Campus, Subang Jaya, Selangor, Malaysia.
- 7 Department of Paediatrics, Faculty of Medicine, University of Malaya, Kuala Lumpur, Malaysia.
- PMID: 30216346
- PMCID: PMC6138391
- DOI: 10.1371/journal.pone.0203469
Background: Breast cancer risk factors have been examined extensively in Western setting and more developed Asian cities/countries. However, there are limited data on developing Asian countries. The purpose of this study was to examine breast cancer risk factors and the change of selected risk factors across birth cohorts in Malaysian women.
Methods: An unmatched hospital based case-control study was conducted from October 2002 to December 2016 in Selangor, Malaysia. A total of 3,683 cases and 3,980 controls were included in this study. Unconditional logistic regressions, adjusted for potential confounding factors, were conducted. The breast cancer risk factors were compared across four birth cohorts by ethnicity.
Results: Ever breastfed, longer breastfeeding duration, a higher soymilk and soy product intake, and a higher level of physical activity were associated with lower risk of breast cancer. Chinese had the lowest breastfeeding rate, shortest breastfeeding duration, lowest parity and highest age of first full term pregnancy.
Conclusions: Our study shows that breastfeeding, soy intake and physical activity are modifiable risk factors for breast cancer. With the increasing incidence of breast cancer there is an urgent need to educate the women about lifestyle intervention they can take to reduce their breast cancer risk.
Conflict of interest statement
The authors have declared that no competing interests exist.
Fig 1. Change of breast cancer risk…
Fig 1. Change of breast cancer risk factors across birth cohorts.
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A case–control study of breast cancer risk and ambient exposure to pesticides : Environmental Epidemiology
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A case–control study of breast cancer risk and ambient exposure to pesticides
Tayour, Carrie a,b ; Ritz, Beate c ; Langholz, Bryan a ; Mills, Paul K. d ; Wu, Anna a ; Wilson, John P. e ; Shahabi, Kaveh e ; Cockburn, Myles a,e,*
a Department of Preventive Medicine, Keck School of Medicine, University of Southern California, Los Angeles, California
b Los Angeles County Department of Public Health, Los Angeles, California
c Departments of Epidemiology and Environmental Sciences, Fielding School of Public Health, University of California, Los Angeles, California
d Department of Medicine, University of California, San Francisco, Fresno, California
e Spatial Sciences Institute, University of Southern California, Los Angeles, California.
Received: 1 May 2019; Accepted 5 September 2019
Published online 30 September 2019
Sponsorships or competing interests that may be relevant to content are disclosed at the end of the article.
The authors declare that they have no conflicts of interest with regard to the content of this report.
The results reported herein correspond to specific aims of grant 5P30ES007048 to investigator M.C. from the US National Institute of Environmental Health Sciences.
Data access: Use of the data may be possible under certain conditions by contacting Myles Cockburn ( [email protected] ).
* Corresponding Author. Address: University of Colorado Cancer Center, 13001 E. 17th Pl., Bldg. 500, 6th Floor, WS49, Aurora, CO 80045. E-mail: [email protected] (M. Cockburn).
This is an open access article distributed under the Creative Commons Attribution License 4.0 (CCBY) , which permits unrestricted use, distribution, and reproduction in any medium, provided the original work is properly cited.
While the estrogenic properties of certain pesticides have been established, associations between pesticide exposure and risk of breast cancer have been inconsistently observed. We investigated the relation between pesticide exposure and breast cancer risk using methods capable of objectively assessing exposure to specific pesticides occurring decades before diagnosis.
A case–control study was conducted to evaluate the risk of postmenopausal breast cancer associated with historic pesticide exposure in California’s Central Valley, the most agriculturally productive region in the United States where pesticide drift poses a major source of nonoccupational exposure. Residential and occupational histories were linked to commercial pesticide reports and land use data to determine exposure to specific chemicals. Cases (N = 155) were recruited from a population-based cancer registry, and controls (N = 150) were obtained from tax assessor and Medicare list mailings.
There was no association between breast cancer and exposure to a selected group of organochlorine pesticides thought to have synergistic endocrine-disrupting potential; however, breast cancer was three times as likely to occur among women exposed to chlorpyrifos compared with those not exposed, after adjusting for exposure to other pesticides including organochlorines (OR = 3.22; 95% CI = 1.38, 7.53).
Organophosphate pesticides, such as chlorpyrifos, have rarely been evaluated in studies of breast cancer risk. Additional research is needed to confirm these findings and to better understand the underlying mechanisms given that chlorpyrifos has been detected in local air monitoring at levels of concern for residents living in the agricultural regions where it is used.
What this study adds
Exposure to pesticides might contribute to breast cancer development, but estimating adult cancer risks associated with previous cumulative exposures presents methodologic challenges, requiring accurate measurements over many decades. We have constructed a comprehensive pesticide exposure assessment using historic pesticide data and geocoded location histories in a case–control study of pesticides and breast cancer. This study suggests that pesticides other than organochlorines, such as the organophosphate chlorpyrifos, may be important for breast cancer risk and that additional research is needed to improve etiologically relevant measures of exposure to protect people who are unknowingly exposed to these chemicals.
Because lifetime estrogen exposure is a key factor in breast cancer development, exposure to endocrine-disrupting pesticides might contribute to breast cancer development. 1–3 While the estrogenic properties of some pesticides have been established, 4–6 results from previous studies of pesticide exposure on breast cancer risk are conflicting: some studies show a positive association, 7–11 while others are null. 12–20
Many previous epidemiologic studies relied upon self-reported exposure based on pesticide usage, occupation, or living on a farm. 11 , 14 , 17–20 Aside from a cohort study which did find some associations for specific pesticides, 7 , 13 the majority of these studies grouped together pesticides with varying toxicologic effects, likely leading to nondifferential exposure misclassification and reported null effects that may have obscured associations with specific chemicals. Other studies used ecologic designs, 16 spatial regression, 8 , 9 or proximity to aggregated pesticide data at only one residential location. 10 , 15 , 20 Studies that use biomarkers to measure pesticide metabolites in serum samples taken near the time of cancer diagnosis may not reflect previous exposures that are most relevant for breast cancer etiology and do not reflect long-term exposure. 21 There is a need for research methodologies that can reconstruct exposures occurring decades before diagnosis and evaluate pesticide-specific exposures on breast cancer risk. 22 , 23
We conducted a case–control study of breast cancer risk from exposure to pesticides using a Geographical Information Systems (GIS)–based method that combines geocoded residential and occupational histories with state pesticide use reports and land use data 24 in California’s highest-ranking counties (Fresno, Tulare, and Kern) for agricultural density and commercial pesticide use in the United States. 25 In highly agricultural regions, pesticide drift from neighboring application sites presents a major source of nonoccupational exposure. 26–30 We evaluated a group of structurally and toxicologically similar 31 organochlorine pesticides with known estrogenic effects that are most likely related to breast carcinogenesis because of their ability to accumulate in adipose tissue and potential to act synergistically (aldrin, chlordane, dicofol, dieldrin, endosulfan, lindane, methoxychlor, and toxaphene). 3 , 5 , 32–36 We also assessed breast cancer risk from exposure to three commonly applied pesticides in the region (chlorpyrifos, diazinon, and 1,3-dichloropropene) detected at levels of concern to human health in air monitoring conducted by the California Department of Pesticide Regulation (CDPR) in 2006 in a Fresno County farming community. 37 Because no regulatory ambient air standards exist for most pesticides, CDPR developed health-based screening levels for 35 pesticides and found that diazinon exceeded its screening level, chlorpyrifos approached its screening level and was frequently detected, and 1,3-dichloropropene exceeded its cancer potency value.
Materials and methods
Cases were recruited from among women with histologically confirmed breast cancer diagnosed in 2007–2008 in the counties of Fresno, Tulare, or Kern from the Cancer Registry of Central California (CRCC), 55–74 years of age, and of non-Hispanic white ethnicity. From 2011 to 2013, cases were recruited by telephone. Among the 328 eligible cases we attempted to recruit, 10 were deceased and four too ill, 123 refused to participate, and we were unable to contact 32. Cases were excluded if they were premenopausal (N = 0) because postmenopausal breast cancer is more likely of hormone-related origin, reported Hispanic ethnicity (N = 2), or had been diagnosed with ovarian, uterine, or other female reproductive cancers before their diagnosis of breast cancer (N = 2). To match control selection criteria (below), cases were excluded if they had not lived in California for at least 5 years (N = 0) or had Parkinson’s disease (N = 0). A total of 155 participants with breast cancer completed the study.
Controls were obtained from another population-based case–control study we conducted in the same geographic area between 2001 and 2011 examining the risk of Parkinson’s disease. Controls lived in California for at least 5 years before the study were at least 35 years old, resided in Fresno, Tulare, and Kern counties, and did not have Parkinson’s disease. Details of control selection are provided elsewhere. 38–40 Controls were recruited from Medicare listings, mailings to a random selection of tax assessor parcel addresses using Internet searches and marketing companies to identify contact information, and from 2009, additional participants were enrolled in person during home visits to randomly selected households. The overall response rate among controls was 46%. 40
From the controls enrolled in the Parkinson’s disease study, we selected postmenopausal women 55–74 years of age of non-Hispanic white ethnicity (N = 208). After excluding women who had been diagnosed with breast cancer (N = 20) ovarian, uterine, or other female reproductive cancers (N = 9), and women who had opted to complete a shortened questionnaire without lifetime residential and occupational histories (N = 29), there were 150 participants included as controls in these analyses.
Source of exposure data
All controls (N = 150) and the majority of cases (N = 111) were interviewed over the telephone, with an additional 44 cases opting to complete a mailed questionnaire with follow-up by telephone to clarify or complete responses. All study participants were mailed a timeline to complete their historic residential and occupational workplace information (addresses and dates) before their telephone interviews. All historic residential and occupational workplace addresses were geocoded using Texas A&M GeoServices geocoder (available at http://geoservices.tamu.edu ) and manually resolved to rooftops or by using additional information from participants such as cross streets and landmarks to more precisely identify a location 41 and improve accuracy of rural locations in particular. 42 We noted the level of “certainty” of each geocoded location and considered addresses to have high geocode certainty if geocoded to the centroid of a building, parcel, nearest parcel, street, or street intersection. Addresses geocoded to the centroid of a zip code, city, county, or state, or those that were unable to be geocoded were considered to have low geocode certainty.
Historic pesticide exposure assessment
Historic pesticide exposures were determined from our GIS-based method that combines state-reported pesticide use data, land use surveys, and geocoded addresses to provide estimates of pesticide exposure within a 500-m buffer around residential and occupational locations. These methods have been described in detail elsewhere. 24 , 40 Briefly, historic pesticide exposures are estimated by linking residential locations with California Pesticide Use Reporting (PUR) data, 43 containing the name of the pesticide active ingredient, the pounds applied, the crop and acreage of the field to which it was applied, the application method, and the date and location. These data were enhanced with land use data from countywide surveys conducted every 6–10 years by California’s Department of Water Resources (DWR), Division of Planning and Local Assistance, 44 to refine the geographical resolution to the crop level as previously reported. 24 , 45
Historic ambient exposure to specific pesticides of interest was calculated by summing the annual density (total pounds of a pesticide’s active ingredients applied per acre) of applied pesticide within a 500-m buffer around each residential and occupational location. 24 This buffer distance was chosen based on studies that found measurable concentrations of pesticides from commercial pesticide application detectable in household dust of neighboring homes. 46–48
Source of covariate data
Telephone interviews were conducted to obtain the covariates age (in years), ever lived on a farm (yes or no), ever worked on a farm (yes or no), education (in years), age at menarche, age at menopause (natural or surgical), number of births (including stillbirth), oral contraceptive use (in years), menopausal hormone therapy use (in years) by type (estrogen only, progesterone only, estrogen plus progesterone, or a mixture of treatments), ever smoked (current, former, and never), ever consumed alcohol at least once a week (yes or no), and vigorous physical activity (defined as the number of hours of strenuous or moderate activity per week). Weight (pounds) and height (feet and inches) at the time of diagnosis or interview were used to calculate body mass index (kg/m 2 ). Neighborhood socioeconomic status (SES) was based on the residential address at the time of diagnosis for cases or at the time of interview for controls using income and occupation information obtained from the 1990 US census data at the block group level and categorized into a quintile score. 49
Participants were asked if they ever personally applied pesticides (yes or no) inside their homes, outdoors in their yards or gardens, on their pets, and whether they had ever hired a professional to spray or fumigate, as well as whether they had ever worked on a farm or with pesticides or fertilizers. To identify occupational pesticide exposure based on self-reported data, other studies have used job-exposure matrices, 50 but only 26 cases and 43 controls reported farming so occupational exposure was based on self-reported “ever” or “never” worked on a farm or worked with pesticides.
Unconditional logistic regression was used to estimate ambient pesticide exposure on the risk of breast cancer in postmenopausal women. Odds ratios (ORs) and 95% confidence intervals (CIs) were calculated for study participants exposed to specific pesticides compared with those not exposed. An individual was considered exposed to a particular pesticide when the pounds per acre of applied pesticide within the buffer area were greater than zero during the period from 1974 until the year of diagnosis for cases and the year of interview for controls. We chose 1974 as the start of our exposure assessment to include all years with complete pesticide information recorded by the State. To account for time between exposure and the development of the disease, we conducted sensitivity analyses excluding 10 and 20 years before diagnosis.
All analyses were adjusted for established breast cancer risk factors including age (continuous), SES (quintiles 1 lowest to 5 highest), body mass index (<25, 25–29, or ≥30 kg/m 2 ), age at menarche (<12, 12, or >12 years), age at menopause (<45, 45–54, or ≥55 years), number of births (0, 1, 2, or ≥3), oral contraceptive use (none, 1–4 years, or ≥5 years), menopausal hormone therapy use (none, estrogen only, progesterone only, estrogen plus progesterone, or a mixture of treatments), and ever consume alcohol at least weekly (yes or no), as well as the number of years lived in Fresno, Tulare, and Kern counties during the exposure assessment time period (continuous). Other factors, including the year of diagnosis, education, ever smoked, vigorous physical activity, ever lived or worked on a farm, and ever personally applied pesticides inside their home, outdoors in their yard or garden, or on their pets, and ever hired a professional to spray or fumigate, were evaluated as potential confounders and were included in the final models if they changed the estimates by >10%. All analyses were conducted using SAS, version 9.3 software (SAS Institute, Inc., Cary, NC).
For the years residential histories had missing location data due to incomplete recall of addresses or addresses that could not be found, we imputed exposures using the average exposures during all years with data for each person. 51 Gaps in workplace histories where women did not report addresses because they were unemployed, at home caring for children, retired, or disabled were imputed with the participant’s residential exposure for that respective time frame (assuming that they most likely resided at home during typical work hours). Pesticide exposure could not be identified for addresses outside of California because the exposure model includes only California PUR data, but participants reported whether any non-California addresses were on farms. We assessed the influence of missing data due to recall and locations outside of California by examining the change in our risk estimates after excluding missing data and conducted sensitivity analyses that included only women who lived in California for at least 30 years between 1974 and their year of diagnosis or interview. We also looked the potential impact of migration in our study by evaluating the influence of demographic factors (age and SES) and disease status among women who moved during our exposure assessment to women who resided in California for at least 30 years and to women who resided in Fresno, Tulare, and Kern counties for at least 30 years.
The institutional review boards at the California Health and Human Services Agency and the University of Southern California approved the study protocol for cases participating in this study. The institutional review board at the University of California, Los Angeles, approved the study protocol for controls used in this study. Informed consent was obtained for all participants.
Cases and controls appeared similar in terms of established breast cancer risk factors such as age, socioeconomic status, education, body mass index, age at menarche, age at menopause, number of births, menopausal hormone therapy use, and vigorous physical activity ( Table 1 ). Cases were more likely to have used oral contraceptives for 5 years or longer (OR = 1.17; 95% CI = 0.70, 1.97). Cases were half as likely to be current smokers (OR = 0.45; 95% CI = 0.20, 1.03) but were more likely to consume alcohol at least weekly compared with controls (OR = 1.74; 95% CI = 1.09, 2.79). Cases were more likely to have lived in Fresno, Tulare, and Kern Counties at least 30 years since the start of our exposure assessment in 1974 and to have lived in California at least 30 years (OR = 1.59; 95% CI = 1.01, 2.51; and OR = 2.52; 95% CI = 1.28, 4.97, respectively). Cases were half as likely to have lived and worked on a farm (OR = 0.44; 95% CI = 0.23, 0.83) ( Table 2 ) or to have worked with pesticides compared with controls, but only three cases and seven controls reported working with pesticides. Cases were more likely to have applied pesticides in their yards or gardens than controls (OR = 1.75; 95% CI = 1.08, 2.82).
When assessing ambient pesticide exposure, the prevalence of exposure at residences and workplaces for the selected group of organochlorines, chlorpyrifos, and diazinon were over 40% among cases and controls ( Table 3 ). After adjusting for breast cancer risk factors, the number of years lived in Fresno, Tulare, and Kern counties, vigorous physical activity (because its inclusion changed the estimates by 19.1%), and exposure to the other pesticides, breast cancer was three times as likely to occur among women exposed to chlorpyrifos at both residences and workplaces compared with those not exposed at either location (OR = 3.22; 95% CI = 1.38, 7.53). Associations more moderate in magnitude were observed between breast cancer and exposure to the group of organochlorine pesticides and to diazinon; however, after adjusting for exposures to other pesticides, in particular chlorpyrifos, the associations were null (OR = 0.98; 95% CI = 0.42, 2.28; and OR = 0.81; 95% CI = 0.35, 1.84, respectively). The vast majority of organochlorine pesticide applications during our exposure assessment were dicofol and endosulfan; and restricting the analyses to only these two organochlorines did not qualitatively change our estimates. There was no increased breast cancer risk for exposure to 1,3-dichloropropene. Results that excluded exposures occurring 10 or 20 years before diagnosis or interview did not qualitatively change the risk estimates. Risk estimates were slightly attenuated for exposure to chlorpyrifos (OR 10 year = 2.78; 95% CI = 1.20, 6.43; and OR 20 year = 3.13; 95% CI = 1.30, 7.52) and remained close to the null for exposure to organochlorines, diazinon, and 1,3-dichloropropene, after accounting for 10- and 20-year latency periods.
Among those reporting that they never lived on a farm, 43.9% of cases and 40.0% of controls were exposed to pesticide drift from one of the selected pesticides at their residence. Among those who reported never working on a farm, 71.6% of cases and 54.7% of controls were exposed to pesticide drift from one of the selected pesticides at their workplace.
Excluding the subjects with substantial missing information in their residential histories did not qualitatively change our estimates. There were three cases and four controls with more than one third of their residential timelines missing. The majority of participants had all residential locations within California during the timeframe of interest (82.0% of cases and 72.7% of controls). Few participants reported that their non-California residences were on farms (three cases and five controls). Restricting analyses to include only those who had lived in California for at least 30 years during our exposure assessment time frame increased estimates for exposure to chlorpyrifos at both residences and workplaces (OR = 3.98; 95% CI = 1.48, 10.72), while estimates remained null for exposures to the other pesticides (data not shown). Participants who migrated out of California or migrated from Fresno, Tulare, and Kern counties during the time period of our exposure assessment did not differ from participants who did not migrate by demographic factors (age and SES) or by disease status (data not shown).
This population-based study examined historic and chemical-specific effects of hormone-related pesticides that are plausibly related to breast cancer in a region of intense agricultural production. We did not observe an association between breast cancer risk and exposure to a group of organochlorines after adjusting for coexposures to other commonly applied pesticides. Conversely, we observed that breast cancer was three times as likely to occur with exposure to the organophosphate chlorpyrifos, one of the three pesticides detected in air monitoring studies at levels of concern to public health (OR = 3.22; 95% CI = 1.38, 7.53). The majority of epidemiologic studies involving pesticides and breast cancer risk have focused on organochlorines, but the increased risk of breast cancer with exposure to the organophosphate chlorpyrifos became stronger after adjusting for exposure to other pesticides including organochlorines.
Previous studies examining exposure to organochlorines have not considered other kinds of pesticides such as chlorpyrifos that may be highly correlated with organochlorines and are driving the breast cancer association. When assessing ambient pesticide exposure, it is usually difficult to distinguish the effects of specific chemicals because applications may be correlated and people can be exposed to multiple chemicals (as is the case with other kinds of toxic air pollutants). For example, among the controls in our study, 54.0% were exposed to both the organochlorines and chlorpyrifos, 24.7% were unexposed to either, and only 21.3% were exposed to one but not the other. Although our chemical-specific exposure model evaluated risk from a group of organochlorine pesticides with potential for synergistic effects, more research is needed to understand possible correlations among applications of pesticides.
Findings from this study suggest that exposure to pesticides other than organochlorines may also affect breast cancer risk. These results support the findings from a large cohort study of farmers’ wives in the Agricultural Health Study, which reported that exposure to chlorpyrifos was one of the pesticides driving a possible breast cancer association (OR = 1.40; 95% CI = 1.0, 2.0) but did not find any associations with entire classifications of organochlorine or organophosphate pesticides. 7 The prevalence of pesticide exposure from ambient sources in this study was over four times the prevalence of self-reported pesticide usage by farmer’s wives, and self-reported exposures do not account for exposures that people may not be aware of but are routinely exposed to, which is often the case with pesticide drift. According to our GIS-based exposure model, among participants in our study who never lived on a farm, 40% or more lived in residences that were within 500 feet of commercial pesticide applications and over 50% were potentially exposed by proximity to their workplace locations.
Evidence is mounting for pesticides besides established organochlorines to act as endocrine disruptors that can increase the risk of breast cancer, particularly for chlorpyrifos. Chlorpyrifos is weakly estrogenic 4 , 5 , 52 and antiandrogenic. 53 , 54 It can affect hormone pathways as an aryl hydrocarbon receptor agonist 55 and induce proliferation of estrogen-dependent breast cancer cells in vitro. 56 At low doses, chlorpyrifos promotes mammary tumor development and alters mammary gland hormone balance in vivo. 57 , 58 More toxicologic research is needed to understand its mechanistic potential with regard to breast cancer risk. The findings from this study, however, support the 2012 regulations that restrict aerial pesticide application of chlorpyrifos to reduce the potential for exposure through pesticide drift. 59
Both chlorpyrifos and diazinon were voluntarily phased out for residential uses in 2000 and 2001, but still used in agriculture. 60 , 61 Although chlorpyrifos and diazinon are both organophosphate pesticides, and as many women were exposed to diazinon as to chlorpyrifos in our study, we did not find an association between diazinon and breast cancer risk after adjusting for exposure to chlorpyrifos. Reasons for this could be due to differing toxicities because chlorpyrifos is cytotoxic at far lower concentrations than diazinon in vitro 62 or due to different exposure potential indicated by the finding that commercial application of chlorpyrifos but not diazinon was significantly correlated with measurements in household dust, even though diazinon was used twice as often. 28
We did not observe an association between breast cancer and 1,3-dichloropropene; however, the prevalence of exposure was low (14.2% of cases and 13.3% of controls exposed at both residences and workplaces). The pesticide 1,3-dichloropropene is a respiratory carcinogen, but its role as a breast carcinogen is unknown. 63
Strengths of this study include GIS-based exposure design that constructs exposure occurring over decades based on individual residential and occupational histories, while controlling for established breast cancer risk factors. Previous studies have estimated pesticide exposure by proximity to applications or crops using addresses at the time of cancer diagnosis with limited information on potential confounders. 8 , 9 , 16 , 19 Our risk estimates based on a single residential address at diagnosis or interview were null for all pesticides considered in these analyses, including exposure to chlorpyrifos (OR = 1.21; 95% CI = 0.56, 2.61), and may underestimate actual risk because they do not account for exposures occurring at workplaces. Only one previous study conducted in Cape Cod, MA, collected residential histories to assess GIS-based proximity to pesticide applications and found no associations; however, the prevalence of pesticide exposures was much lower than observed in our study, and exposures were grouped by land use type instead of by specific pesticide of interest. 12
Exposure in this study was based on reported address histories rather than self-reported pesticide usage, reducing the potential for recall bias. A study conducted in Australia found that the association between breast cancer risk and self-reported “noticing of pesticide spray drift” was strongly confounded by participants’ belief in whether or not pesticides caused breast cancer (OR = 1.47; 95% CI = 1.15, 1.87 among believers and OR = 0.94; 95% CI = 0.51, 1.74 among nonbelievers). 64
Our GIS-based method also reduces the potential for selection bias from differential participation as a result of concerns about exposures in the environment. Selection bias may still be a concern because cases were recruited from a population-based cancer registry while controls were obtained for another population-based study in the same location. Although we started interviewing controls earlier than cases, the median and distribution of dates of interviews are similar between cases and controls ( Table 1 ). A time difference for enrollment of cases and controls could have a potential impact on the calculations of average annual exposure if there was a rapid change in the use or application of a pesticide that occurred near the years of diagnosis or interview, but the risk estimates were only slightly attenuated after accounting for 10- and 20-year latency periods. Controls were more likely to have lived or worked on a farm than cases and as a result would be expected to have higher likelihood of exposure to pesticides near their residences or workplaces, thus biasing our estimates toward the null; and yet, we still observed a strong association to one of the pesticides of interest. Cases, on the other hand, were more likely to have lived in Fresno, Tulare, or Kern counties longer than controls and, therefore, may have had more opportunity to be exposed to ambient pesticides in the region. We adjusted the analyses for the number of years lived in Fresno, Tulare, or Kern counties but still observed chemical-specific effects. Women who migrated during the exposure assessment did not differ from women who did not migrate by age, SES, or disease status; thus, migration is not likely to have differentially impacted our overall findings.
It is important to note that breast cancer cases participating in this study are of surviving cases. Participant cases were similar in age and SES to the population-based registry from which they were recruited but were less likely to have late-stage disease (data not shown). If there is a dose–response effect of pesticide exposure on severity of disease, then we are more likely to have recruited women with lower exposure, which would have resulted in an underestimation of the effects presented here. The geocode certainty of the historic addresses was similar for cases and controls for the period of our exposure assessment from 1974 until the year of diagnosis or interview. There were 92.3% of cases and 96.7% of controls residing 50% or more of the years during the time period at residential addresses having high geocode certainty and 78.1% of cases and 83.3% of controls working 50% or more of the years during the time period at workplace addresses having high geocode certainty. This suggests that the certainty of the geocoding is not likely to account for difference in the estimated effects.
Estimating adult cancer risks associated with previous cumulative exposures present methodologic challenges for epidemiologic studies because it requires accurate measurements over lifetime and decades. The GIS-based methods presented here likely reduce exposure misclassification compared with estimates based on self-reported pesticide use. We have constructed a more comprehensive exposure assessment using historic data than has been done previously; however, a larger study is needed to confirm the chemical-specific associations we report and to examine different levels of exposure as well as potential dose–response relations.
This study suggests that pesticides other than organochlorines, such as chlorpyrifos, may be important for breast cancer risk and that additional research is needed to improve etiologically relevant measures of exposure to protect people who are unknowingly exposed to these chemicals in the air.
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Breast cancer; Pesticides; Geographical Information Systems; Exposure Assessment
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A multi-center population-based case–control study of ovarian cancer in African-American women: the African American Cancer Epidemiology Study (AACES)
- Joellen M Schildkraut 1 ,
- Anthony J Alberg 2 ,
- Elisa V Bandera 3 ,
- Jill Barnholtz-Sloan 4 ,
- Melissa Bondy 5 ,
- Michelle L Cote 6 ,
- Ellen Funkhouser 7 ,
- Edward Peters 8 ,
- Ann G Schwartz 6 ,
- Paul Terry 9 ,
- Kristin Wallace 2 ,
- Lucy Akushevich 1 ,
- Frances Wang 1 ,
- Sydnee Crankshaw 1 &
- Patricia G Moorman 1
BMC Cancer volume 14 , Article number: 688 ( 2014 ) Cite this article
Ovarian cancer (OVCA) is the leading cause of death from gynecological cancer, with poorer survival for African American (AA) women compared to whites. However, little is known about risk factors for OVCA in AA. To study the epidemiology of OVCA in this population, we started a collaborative effort in 10 sites in the US. Here we describe the study and highlight the challenges of conducting a study of a lethal disease in a minority population.
The African American Cancer Epidemiology Study (AACES) is an ongoing, population-based case–control study of OVCA in AA in 10 geographic locations, aiming to recruit 850 women with invasive epithelial OVCA and 850 controls age- and geographically-matched to cases. Rapid case ascertainment and random-digit-dialing systems are in place to ascertain cases and controls, respectively. A telephone survey focuses on risk factors as well as factors of particular relevance for AAs. Food-frequency questionnaires, follow-up surveys, biospecimens and medical records are also obtained.
Current accrual of 403 AA OVCA cases and 639 controls exceeds that of any existing study to date. We observed a high proportion (15%) of deceased non-responders among the cases that in part is explained by advanced stage at diagnosis. A logistic regression model did not support that socio-economic status was a factor in advanced stage at diagnosis. Most risk factor associations were in the expected direction and magnitude. High BMI was associated with ovarian cancer risk, with multivariable adjusted ORs and 95% CIs of 1.50 (0.99-2.27) for obese and 1.27 (0.85- 1.91) for morbidly obese women compared to normal/underweight women.
AACES targets a rare tumor in AAs and addresses issues most relevant to this population. The importance of the study is accentuated by the high proportion of OVCA cases ascertained as deceased. Our analyses indicated that obesity, highly prevalent in this population (>60% of the cases), was associated with increased OVCA risk. While these findings need to be replicated, they suggest the potential for an effective intervention on the risk in AAs. Upon completion of enrollment, AACES will be the largest epidemiologic study of OVCA in AA women.
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Each year, over 22,000 new ovarian cancer (OVCA) cases are diagnosed in the United States, accounting for approximately 4% of cancers in women [ 1 ]. Epithelial OVCA is the most lethal gynecologic malignancy among both African American (AA) and white women, predominantly due to the absence of sufficiently accurate screening tests, resulting in most women having advanced disease at the time of clinical presentation [ 2 ]. Although incidence is lower among AA women than in white women (9.8 vs. 13.0 cases/100,000), 5-year relative survival is worse for AA women than white women across all ages (36% vs 44%) [ 3 ]. In addition, AA women tend to get the disease at a younger age (61 versus 64 years) [ 4 ].
Reasons for poorer survival among AA women are unknown [ 5 ], but are likely multi-factorial, including differences in treatment, access to care and comorbidities, as well as more aggressive presentation [ 6 – 9 ]. Preliminary data from our group and others suggest AA and white women with OVCA differ in the distribution of intrinsic subtypes associated with poorer outcome of ovarian cancer [ 10 ], in the prevalence of certain reproductive [ 11 – 13 ] and genetic risk factors [ 14 – 16 ], and in the receipt of guideline-recommended treatment [ 9 ].
Although currently available evidence is suggestive of differences in risk and prognostic factors between AA and white women, the evidence-base is limited. For example, the three epidemiologic studies reporting on risk factors for OVCA in AA women [ 11 – 13 ] all had fewer than 150 cases, reflecting the relatively small number of OVCA cases diagnosed in AA women and the barriers to enrolling a large number of cases from a single geographic location. With the goal of improving our understanding of factors that affect risk and survival among AA women with OVCA, we established the African American Cancer Epidemiology Study (AACES), an ongoing, multi-state, multi-center, population-based case–control study. The aims of this study include assessment of associations with established risk factors, evaluation of genetic susceptibility, characterization of tumor biology and evaluation of socioeconomic and behavioral factors that may affect prognosis through delays in diagnosis and treatment. The purpose of this paper is to describe the study design, challenges in recruitment, and the study population enrolled thus far.
Study design, subject identification and enrollment
The 10 AACES sites include institutions that are located in geographic regions with a relatively high density of AAs in the population and that have the capability of rapidly identifying newly diagnosed cases of OVCA. The geographic regions are largely concentrated in the southern US (Alabama, Georgia, Louisiana, North Carolina, South Carolina, and Tennessee), and also include the southwest (Texas), midwest (Michigan and Ohio), and mid-Atlantic region (New Jersey). The study protocol, consent forms and questionnaire were approved by the Institutional Review Boards (IRB) at Duke University Medical Center, Baylor College of Medicine, Case Western Reserve University School of Medicine, Louisiana State University, Robert Wood Johnson Medical School/Rutgers Cancer Institute, Wayne State University, the University of Alabama-Birmingham, the Medical University of South Carolina and the University of Tennessee-Knoxville. Additionally, the protocol was approved by central cancer registries in the states of Alabama, Georgia, North Carolina, South Carolina, Tennessee and Texas, SEER (Surveillance, Epidemiology and End Results) registries in New Jersey, Louisiana, and the Detroit metropolitan area, and 9 individual hospital systems in Ohio. Accrual of cases and controls began December 1, 2010 and will be completed by the end of 2015.
Eligible cases include all AA women aged 20 to 79 years newly diagnosed with a histologically confirmed invasive epithelial OVCA since December 1, 2010. Race (full or mixed AA) is based on self-report. Cases are identified through rapid case ascertainment systems that utilize state cancer registries, SEER registries or gynecologic oncology departments at individual hospitals. The physicians of each eligible patient are contacted to request permission to approach the patient. According to the protocol required at each site, either written consent is obtained or consent to contact the women is assumed if the physician does not object within a reasonable period of time (2 to 3 weeks) after notification.
Control identification began in May 2011. An outside contractor (Kreider Research and Consulting) uses list-assisted, random-digit dialing (RDD) to select control women who self-identify as AA race (full or mixed race), and are matched to cases by 5-year age category and state of residence. Phone numbers are chosen from both landline and cellular telephone exchanges. Eligibility is confirmed through a series of screening questions, and contact information for eligible controls is forwarded to the study coordinating center at Duke. Women with a previous diagnosis of OVCA are excluded as are women who have had a bilateral oophorectomy. Only subjects able to complete an interview in English are included.
Cases approved for contact by their physicians and controls identified by the RDD contractor are sent an introductory letter and study brochure with an identifiable study logo. The link to a study website and a toll-free number are also provided to potential study subjects who may have questions about the study. Verbal informed consent is provided by each participant at the time of the telephone interview, and written informed consent is obtained for collection of biospecimens and medical records.
Data and biospecimen collection
Approximately 1–2 weeks after sending an introductory letter, a trained interviewer contacts the potential study participant by telephone to answer questions and schedule the interview. Women who agree to participate are contacted by telephone at the agreed upon time, and after review of the consent form, a computer-assisted telephone interview (CATI) is administered. The questionnaire includes detailed questions on demographic characteristics, reproductive, gynecologic and medical history, exogenous hormone use (any type of hormone replacement therapy (HRT) and oral contraceptives (OCs)), family history of cancer and lifestyle characteristics such as smoking, alcohol consumption, and physical activity. There are also questions that address constructs that are of particular relevance for this study population including perceived discrimination, cultural and folk beliefs, access to medical care, trust of health care providers and religiosity. A more detailed description of the questionnaire content is provided in Table 1 . The CATI surveys for cases are conducted by interviewers at Duke, with the exception of cases from Detroit for which registry policy requires that the interview be completed by a local interviewer. Controls from all sites are interviewed by the interviewers based at Duke and the Karmanos Cancer Institute in Detroit. To increase response rates, an abbreviated, short interview is offered if the study subject expresses a concern about her time spent on the telephone.
Food frequency questionnaire
A self-administered food frequency survey (the Block 2005 Food Frequency Questionnaire) is mailed to the study subjects with other study documents. Subjects complete the food frequency questionnaire on their own, but if needed, the interviewer will assist with its completion.
In addition to the questionnaires, all study subjects are asked to provide a blood or saliva specimen for DNA analyses. After receiving a signed consent form for specimen collection at the Duke study coordinating center, the information is forwarded to the contractor responsible for specimen collection, Examination Management Service, Inc. (EMSI). EMSI has offices nationwide and arranges for a trained phlebotomist to meet each participant at her home or other convenient location to obtain a biospecimen and anthropometric measurements (height, weight and waist and hip circumferences). Each participant is asked to provide a 30 ml blood sample, however, if she is unable or unwilling to do so, she is asked to give a saliva sample using an Oragene® kit. Oragene® kits are mailed directly to participants who consent to give a biospecimen but do not wish to have a home visit.
Women with OVCA also are asked to grant permission for the study to obtain a formalin-fixed, paraffin-embedded (FFPE) tumor block from their primary tumor. Pathology reports and tumor blocks or sections are requested from pathologists, and the FFPE tumor blocks are cut according to study protocol for all cases. A centralized pathology review for all cases is conducted at Duke by the study pathologist, a specialist in gynecologic cancers.
All study participants are remunerated for their time at two benchmarks during enrollment: 1) upon completion of the telephone interview and 2) upon receipt of either a blood or saliva specimen.
Cases are followed on an annual basis. A follow-up telephone survey is administered by Duke staff and includes questions on insurance, updates to medical history, occupational status, medication use, quality of life, social support, stress and other factors that may be related to outcome. Additionally, medical records are requested to obtain diagnostic, treatment and outcomes information.
Variables and coding
Demographic characteristics include age at diagnosis for cases and age at interview for controls (categorized as 20- < 40, 40- < 50, 50- < 60, 60- < 70, 70- < 80 years), education (≤high school, some post-high school training, college/graduate degree), annual income (<$10K, $10K- < $25K, $25K- < $50K, $50K- < $75K, ≥$75K), current medical insurance (none, Medicaid, Medicare, other), and access to a private physician (yes, no). Body mass index 1 year before diagnosis (cases)/interview (controls) (BMI) is categorized as <25, 25- < 30, 30- < 35 or ≥35 kg/m 2 . Additional risk factors include parity (0, 1–2, ≥3), months of OC use (never to <3, 3- < 36, 36- < 60, ≥60 months), use of any HRT (ever, never), age at menarche (<12, 12- < 13, ≥13 years), tubal ligation (yes, no), menopausal status (pre-menopausal or postmenopausal), and any first- degree relative with OVCA or breast cancer (yes, no). Premenopausal women are those who are still experiencing menstrual cycles at the date of diagnosis/interview, regardless as to whether the cycles are the usual cycle pattern or missed/interrupted periods. Women who are taking birth control pills are also classified as premenopausal. Women are classified as menopausal if menstrual periods have stopped or both ovaries have been removed. For women < 50 years of age who have had a hysterectomy and do not have menopausal symptoms or have symptoms for less than two years are classified as premenopausal. Women who have had a hysterectomy who are less than 50 years of age and have had symptoms for at least two years or are 50 years of age older are classified as postmenopausal.
Time from diagnosis to ascertainment is calculated as the difference between the date at diagnosis from the pathology report and the date the information is received at the Duke study office. We calculated the number of days from diagnosis to interview as the difference between the date of diagnosis and the date when the telephone interview was completed.
We used descriptive statistics to summarize the characteristics of surveyed AA women. Values are expressed as n (%), means or medians and interquartile ranges. To compare risk factor characteristics between cases and controls we calculated age-adjusted and multivariable-adjusted odds ratios (ORs) and 95 percent confidence intervals (CIs) using unconditional logistic regression analyses. Comparisons of characteristics of responders and non-responders were evaluated with chi-square tests.
Response rates were calculated according to the formula:
Cooperation rates, defined as the proportion of completed interviews among eligible women actually contacted, were calculated according to the formula:
Since this study is ongoing, we calculate the response rate two ways; 1) we assume all pending subjects participate in the study and include the pending subjects in the numerator and 2) we assume all pending subjects decline the study and calculate the rate with the pending subjects in the denominator only.
We collected and managed the subject accrual data using REDCap electronic data capture tools hosted at Duke University [ 17 ]. Statistical analyses were performed using SAS version 9.3 (SAS Institute, Cary, NC).
Study enrollment began in May 2011, with cases being deemed eligible if they were diagnosed since December 2010. Our goal is to enroll 850 AA women with invasive epithelial OVCA and 850 controls by December 2015.
As of April 8th, 2014, we identified 1,055 women newly diagnosed with OVCA, of whom 940 met study eligibility criteria. As of this date, 403 newly diagnosed OVCA cases have completed an interview and 68 cases are still pending. Non-participation was due to physician refusals (n = 10), subject refusals (n = 203), death (n = 141) and inability to contact (n = 117). Assuming all pending cases decline to participate in the study, the overall response rate would be 43%. If all pending cases choose to participate the response rate would be as high as 50%. Among cases that we were able to contact, the cooperation rate is 66.5%.
Among 1,334 potential controls identified through RDD, 1,284 met the eligibility criteria. Interviews have been completed with 639 controls and 150 are pending. Non-participation was due to subject refusals (n = 252), inability to contact (n = 240) and death (n = 3). If all pending subjects decline participation in the study, the overall response rate among controls would be 50%, and if all pending subjects agree to participate, the response rate would be 61%. Among potential controls that we were able to contact, the cooperation rate is 72%.
Once participants agreed to be interviewed, the majority completed all components of the study. Among women agreeing to the telephone survey, most (93% of cases and 98% of controls) completed the long questionnaire, which is designed to be completed in approximately 1 hour. A shorter, 15-minute survey, which is offered as an option for women who are unwilling or unable to complete the long questionnaire, was completed by 30 cases and 16 controls.
More than 93% of the women interviewed have also completed the 110-item food frequency questionnaire. Most food frequency questionnaires were self-completed; however, the interviewers completed it on the phone for 15 cases and 24 controls who requested assistance.
To date, 284 (70%) of the enrolled cases and 454 (71%) of the enrolled controls have provided a blood and/or saliva sample. Only 3.7% of the cases and 6.0% of the controls did not consent to biospecimen collection. There are 104 cases and 147 controls who completed the questionnaire and are pending biospecimen collection. Of the samples collected 79% of cases and 78% of controls donated a blood sample.
Time to ascertainment/interview
The goal of rapid case ascertainment is to identify cancer cases as soon as feasibly possible after diagnosis to minimize loss to death. This is particularly important for diseases like OVCA that have a high fatality rate. Underscoring the severity of OVCA among African-American women, among eligible cases in our study, 15% were deceased at the time of ascertainment.
We examined the time between diagnosis and ascertainment for all identified cases and by participation status. For all OVCA cases, the median time from diagnosis to the receipt of the pathologic information at the study office was 134 days (Table 2 ). When omitting the first year of accrual to allow for the maturation of the rapid case ascertainment protocols, median days from diagnosis to the identification of cases decreased to 91 days. The median time between diagnosis and ascertainment was longer for non-responders than responders. This difference was especially pronounced for the women who were deceased before they could be contacted. Excluding the first year of accrual, the median days from diagnosis to interview was 145 days or approximately 5 months. More than three-quarters of the OVCA cases are interviewed within 9 months of diagnosis.
Responder versus non-responder characteristics
Among eligible cases, only a limited number of variables are available to evaluate differences between the 403 responders and 464 non-responders, of which 139 were deceased at ascertainment (Table 3 ). The responders, on average, were younger than the non-responders, 57 years (standard deviation (SD) = 11.2 years) compared to 61 years (SD = 11.2 years) (p <0.0001). The age at diagnosis for live and deceased non-responders, 60.8 years (SD = 11.2) and 61.2 years (SD = 11.1), respectively, were not statistically different (p = 0.69). Most notably, a smaller proportion of the responders were found in the oldest age categories, 60–69 years and 70–79 years compared to both live and deceased non-responders who appeared to have a similar distribution of age at diagnosis. Stage was more advanced among the non-responders compared to responders, with 84. 2% of deceased non-responders and 61.5% of the live non-responders assigned a stage III/IV at diagnosis compared to 52.2% of the responders. Although the histologic subtype distribution of the responders was similar to that of the live non-responders (p = 0.37), a significant difference in the histologic subtype distribution between responders and deceased non-responders was found. In particular, the serous and endometrioid subtypes were less common among the deceased non-responders compared to both responders and live non-responders. Over 54% of the deceased non-responders were classified as having histology of ‘other’ compared to 15.6% and 21.7% of the responders and live non-responders with the majority of tumors in this category classified as carcinomas NOS (87% overall and 90% of the deceased non-responders, data not shown). The distribution of tumor grade is similar among responders and live non-responders, with just under 75% being poorly-differentiated among both groups. The proportion of poorly-differentiated tumors among the deceased non-responders is higher with approximately 81% classified as poorly-differentiated. However, the distribution of grade was not found to be significantly different from that of the responders (p = 0.20). Although there is only a small proportion of cases with missing histology and stage at diagnosis data, 28% and 55% of live and deceased non-responders versus 17% of responders have missing data for tumor grade. These statistics are preliminary since centralized pathology review is ongoing and grade is missing for a large number of the subjects.
The mean age at diagnosis (based on the date of the pathology report)/age at interview of the cases and controls, respectively, was 57.4 years (SD = 11.2 years) and 54.1 years (SD = 11.8 years) (p < 0.0001), respectively. Additional comparisons of demographic characteristics and epidemiologic risk factors between cases and controls are found in Table 4 . Although the study is designed to frequency match controls to cases by age, there were more cases in the 70–79 year age group than controls, 16.1% versus 8.6% and fewer cases in the youngest age category of 20–39 years compared to controls, 6.5% and 12.4%, respectively. Going forward measures are being taken to focus control identification and recruitment in these older age categories. Response rates for the cases were lower for those 60 years of age and above at diagnosis compared to those below 60 years of age at diagnosis. The age at interview did not appear to be related to response rate among controls (data not shown).
Age-adjusted and multivariable adjusted analyses of well-established OVCA risk factors revealed associations that were in the expected direction, although not all were statistically significant (Table 4 ). Few differences in age-adjusted ORs compared to multivariable-adjusted ORs are seen. As compared to controls, cases were less likely to have used OCs with a weak inverse trend in reduced risk with longer duration of use. Compared to controls cases also were less likely to have had a tubal ligation, but were more likely to be nulliparous, have a relative with breast or ovarian cancer, or have used any type of HRT. Case–control associations with BMI 1 year prior to the referent date of 30- < 35 kg/m 2 , parity > 3, months of OC use, and family history of breast or ovarian cancer approached or were statistically significant.
In Table 4 , preliminary case–control comparisons of variables related to socio-economic status revealed that controls were more likely to report having some post high school training or a college education compared to cases. Although not reaching statistical significance, controls were more likely to have an annual income of $75,000 or more and more controls reported having access to a private physician compared to cases. No difference was found with the current insurance in cases compared to controls although there was a tendency for cases to be more likely to report they had ‘Medicaid’ and less likely to report ‘Other Insurance’ versus ‘No Insurance’ compared to controls.
In Table 5 , we present both age-adjusted and multivariable adjusted ORs and 95% CIs for case–control associations with BMI, education and income for advanced (III/IV) versus early (I/II) stage at diagnosis. Few differences in the age-adjusted and multivariable-adjusted ORs are seen, with the exception of annual income, where the multivariable-adjusted ORs show an inverse association with early stage ovarian cancer cases but not advanced stage cases compared to controls. A case-only analysis using multivariable logistic regression, adjusting for age at diagnosis, does not support that indicators of socio-economic status along with BMI are associated with advanced stage at diagnosis, an important prognostic indicator (data not shown).
The progress to date on the AACES study demonstrates both the importance and the challenge of studying OVCA in AA women. The high proportion of women who are deceased before they could be enrolled in the study underscores the severity of the disease in this population and the urgent need to better understand factors that affect its etiology and prognosis. The high frequency of rapidly fatal disease also highlights one of the challenges of conducting an epidemiologic study of OVCA in this population.
The possible selection bias that can result from low participation rates in case–control studies is a topic of high concern and has been discussed repeatedly in the literature [ 18 , 19 ]. In addition to secular trends of declining participation rates across all types of studies, [ 18 ] AACES faces the additional challenges of the typically lower participation rates among minority populations and lower participation rates among cases due to advanced disease.
Although, many case–control studies report higher response rates among cases than controls [ 13 , 19 ], the opposite is true in AACES, which is likely attributable to disease severity. As our data show, non-responders, particularly those patients who are deceased at ascertainment, are more likely to be diagnosed with advanced stage disease. Although no differences in tumor histology or grade were observed in responders compared to live-non-responders, differences were found in the deceased non-responders. These are likely due to a higher proportion of tumors defined as carcinoma NOS and may explain why there are fewer serous and endometrioid cases among this group of women, who may have not received the same level of care or pathologic scrutiny.
Despite working with institutions that have established methods for rapid case ascertainment, including three SEER sites, we have a remarkably high proportion of cases deceased at the time of accrual (15% of the total eligible). The proportion of deceased cases in AACES is approximately the same as what we observed among AA women with invasive OVCA in a previous population-based study of OVCA in North Carolina (14%) [ 13 ] (unpublished data). Notably, the overall proportion of deceased cases in that study was 4%, but was approximately three times higher in AAs than whites. In AACES, we found a longer length of time between date of diagnosis and ascertainment among those deceased as compared to those who eventually enrolled in the study, which may partially account for the overall high proportion of deceased patients. In addition, we suspect the relatively high proportion of cases that we were unable to contact (12% of eligible cases) also may be related to disease severity as we have heard anecdotal accounts that some women have had to move in with someone else to receive care after their diagnosis. Although it is possible that the high prevalence of BMI and low socioeconomic status may contribute to the high proportion of deaths at ascertainment, we were not able to detect an association between these factors and advanced stage at diagnosis, an important prognostic indicator. BMI and factors related to socio-economic status were not available for the non-responders, limiting our ability to assess how these factors may have influenced the proportion of deaths among eligible cases prior to ascertainment.
Our ability to evaluate selection bias among the OVCA cases was limited, with data available for only a few patient characteristics for the non-responders. Overall, the non-responders are older and appear to have more advanced disease, and likely a poorer prognosis, compared to responders. This finding is found among similarly designed studies as AACES, although not consistently [ 19 ].
Because the target population is AA women with OVCA, a multi-state, multi-center, case–control study was the only viable study design that would permit the accrual of sufficient numbers of cases and controls in a reasonable period of time. In spite of the limitations and challenges of AACES, epidemiologic risk factors appear to be distributed as would be expected from previous published reports, with no history of OC use, nulliparity, no history of tubal ligation and a family history of breast or OVCA more common among cases than controls [ 13 , 20 , 21 ]. Although more refined analyses are required in a larger sample, a noteworthy finding is the increased risk associated with a BMI greater than 30 kg/m 2 with ORs in the range of 1.4 to 1.5. The high prevalence of obese and severely obese women in this population (~55% of the control women) suggests reducing BMI may be an effective means of preventing OVCA among AAs.
Upon completion, AACES will represent the largest study to date of OVCA in AA women, with more than five times as many cases as in any previous study. The number of AA cases that we will enroll will exceed even the number of cases from large consortia such as the Ovarian Cancer Association Consortium (382 invasive cases in women of African ancestry across more than 60 individual studies in the U.S. and Europe) or the African American Cohort Consortium (~240 cases in 5 cohorts) (personal communication J. Palmer). The major strengths of the AACES study are that it uses standard protocols for data collection across 10 geographic regions in the U.S. encompassing both rural and urban regions and it collects data that are of particular relevance for AA women, including perceived discrimination, access to health care, and cultural and folk beliefs, that have not been collected in previous studies of OVCA.
Although the main limitation of the AACES appears to lie in the possible but unavoidable selection bias, the large study sample and the information collected represent a rich opportunity for studying an uncommon cancer in a minority population. The AACES telephone surveys and food frequency questionnaires, the biospecimens and the medical record data will provide an unprecedented resource, both in breadth and depth, for studying OVCA in women of African ancestry in the U.S.
AACES participants represent an understudied population, with a disproportionate number of women of lower socio-economic status. It is well documented that women of African descent in the U.S. experience significant health disparities leading to poorer outcomes for many diseases. We are confident that AACES will lead to an increased understanding of the factors that influence risk and overall outcome of this disease among AA women.
Most of the epidemiologic risk factor associations in AA women were found to be similar to those reported for white women. Our data support that obesity, found to be prevalent in more than 60% of the cases, was significantly associated with increased OVCA risk. This finding suggests the potential for an effective intervention on the risk in AAs. A high proportion of women with OVCA was deceased and among these women, a high proportion was diagnosed at an advanced stage. Since early stage cancers have a better survival, there is a clear need to better understand causes of advanced stage cancer diagnoses and to address access to care issues in this population. Upon completion of enrollment, AACES will be the largest epidemiologic study of OVCA in AA women, providing a unique opportunity to increase our knowledge of the epidemiology of OVCA in AA women.
- African American
African American Cancer Epidemiology Study
Body mass index
Computer assisted telephone interview
Hormone replacement therapy
Institutional Review Board
- Ovarian cancer
Surveillance, Epidemiology and End Results.
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The pre-publication history for this paper can be accessed here: http://www.biomedcentral.com/1471-2407/14/688/prepub
We would like to acknowledge the AACES interviewers, Christine Bard, LaTonda Briggs, Whitney Franz (North Carolina) and Robin Gold (Detroit). We also acknowledge the individuals responsible for facilitating case ascertainment across the ten sites including: Jennifer Burczyk-Brown (Alabama); Rana Bayakly and Vicki Bennett (Georgia); the Louisiana Tumor Registry; Lisa Paddock and Manisha Narang (New Jersey); Diana Slone, Yingli Wolinsky, Steven Waggoner, Anne Heugel, Nancy Fusco, Kelly Ferguson, Peter Rose, Deb Strater, Taryn Ferber, Donna White, Lynn Borzi, Eric Jenison, Nairmeen Haller, Debbie Thomas, Vivian von Gruenigen, Michele McCarroll, Joyce Neading, John Geisler, Stephanie Smiddy, David Cohn, Michele Vaughan, Luis Vaccarello, Elayna Freese, James Pavelka, Pam Plummer, William Nahhas, Ellen Cato, John Moroney, Mark Wysong, Tonia Combs, Marci Bowling, Brandon Fletcher (Ohio); Martin Whiteside (Tennessee) and Georgina Armstrong and the Texas Registry, Cancer Epidemiology and Surveillance Branch, Department of State Health Services.
The AACES study was funded by NCI (CA142081-01A1). Additional support was provided by Metropolitan Detroit Cancer Surveillance System (MDCSS) with federal funds from the National Cancer Institute, National Institute of Health, Dept. of Health and Human Services, under Contract No. HHSN261201000028C and the Epidemiology Research Core, supported in part by NCI Center Grant (P30CA22453) to the Karmanos Cancer Institute, Wayne State University School of Medicine.
Authors and affiliations.
Duke Cancer Institute, Department of Community and Family Medicine, Duke University Medical Center, Durham, NC, USA
Joellen M Schildkraut, Lucy Akushevich, Frances Wang, Sydnee Crankshaw & Patricia G Moorman
Hollings Cancer Center and Department of Public Health Sciences, Medical University of South Carolina, Charleston, SC, USA
Anthony J Alberg & Kristin Wallace
Cancer Prevention and Control Program, Rutgers Cancer Institute of New Jersey, New Brunswick, NJ, USA
Elisa V Bandera
Case Comprehensive Cancer Center, Case Western Reserve University School of Medicine, Cleveland, OH, USA
Cancer Prevention and Population Sciences Program, Baylor College of Medicine, Houston, TX, USA
Wayne State University School of Medicine, Department of Oncology, Karmanos Cancer Institute Population Studies and Disparities Research Program, Detroit, MI, USA
Michelle L Cote & Ann G Schwartz
Division of Preventive Medicine, University of Alabama at Birmingham, Birmingham, AL, USA
Epidemiology Program, Louisiana State University School of Public Health, New Orleans, LA, USA
Departments of Public Health and Surgery, University of Tennessee-Knoxville, Knoxville, TN, USA
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Correspondence to Joellen M Schildkraut .
The authors declare that they have no competing interests.
Data acquisition: AA, MB, EB, PM, JMS, EF, J B-S, EP, AS, MC, PT, SC. Data Management/Data analysis: LA, FW. Manuscript preparation: JS, PM, EB, AA, J B-S. All authors read and approved the final manuscript.
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Schildkraut, J.M., Alberg, A.J., Bandera, E.V. et al. A multi-center population-based case–control study of ovarian cancer in African-American women: the African American Cancer Epidemiology Study (AACES). BMC Cancer 14 , 688 (2014). https://doi.org/10.1186/1471-2407-14-688
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Published : 22 September 2014
DOI : https://doi.org/10.1186/1471-2407-14-688
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Case-Control Studies of Cancer Screening: Theory and Practice
We thank Drs. Susan M. Moss and DeAnn Lazovich for their useful discussions and helpful comments on this subject during the preparation of the manuscript.
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Kathleen A. Cronin, Robert J. Connor, Philip C. Prorok, Douglas L. Weed, Case-Control Studies of Cancer Screening: Theory and Practice, JNCI: Journal of the National Cancer Institute , Volume 90, Issue 7, 1 April 1998, Pages 498–504, https://doi.org/10.1093/jnci/90.7.498
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This review summarizes methodologic theories for the design of cancer screening case-control studies and examines the methods applied in studies published in English from 1980 through 1996. In addition to summarizing state-of-theart methodologic approaches, we identify areas where obvious gaps exist between theory and practice, and we recommend potential areas where theory and methodology may need further development. In particular, we focus on three major areas: 1) the selection of case and control subjects, 2) the definition of exposure (i.e., exposure to the screening test), and 3) bias. Each area is considered carefully by summarizing current theory, reviewing cancer screening applications, and linking recommended methodologic approaches to those used in practice to identify areas where inconsistencies exist. In general, we found methodologic theory and practice in this field of research to be consistent. However, discrepancies were identified in the area of exposure definition, including the use of screening frequency and the use of a detectable, curable preclinical phase for case subjects as the exposure measures. Even when recommended methods were followed, a number of difficulties arose in practice. Specific concerns included the ability to carry out the following: identifying all case subjects within a source population, defining eligibility criteria to ensure that case and control subjects had equal access to screening during the exposure period, distinguishing between symptomatic and diagnostic tests, and controlling for self-selection bias. Careful scrutiny is warranted in all aspects of the design of cancer screening case-control studies, and caution is advised in the interpretation of study results.
Ideally, the effectiveness of a screening program is demonstrated through randomized clinical trials before the screening test is introduced to the general population. However, in an era where many potential screening tests are being developed and both medical practitioners and the public play larger roles in requesting new tests, clinical trial evidence may not be available. Case-control studies are one way to examine the efficacy of screening in the absence of clinical trial evidence. These studies use an odds ratio, representing the rate of exposure in case subjects divided by the rate of exposure in control subjects, to estimate efficacy ( 1 ) .
Case-control studies are able to study rare events using a small number of individuals and have some logistical advantages over randomized trials. Not only are they less costly than clinical trials, but they may also be applied in situations in which a screening test has become widespread in the general public before the test's effectiveness has been determined by clinical trials. Despite these advantages, case-control studies also have important drawbacks. Their retrospective nature and lack of randomization make them more susceptible to biases. Compared with trials, the data obtained may be of lesser quality and completeness. The increasing use of case-control methodologies, coupled with concerns about their validity, suggest that careful scrutiny of these methods is warranted.
The theory and practice of case-control studies to evaluate the efficacy of screening have been evolving over the past two decades. During this time, methodologic theories have developed concurrently with their application in practice. In this review, we present a comprehensive summary of the methodologic theory up to the present. Emphasis is placed on issues and potential biases that are unique to screening efficacy case-control studies. In addition, we compare methods described in theoretical papers to the methods used in practice. Because it is a rapidly evolving field, currently recommended methods may postdate the application papers discussed. Therefore, our work is not meant as a criticism of application papers. When possible, we point out whether differences are due to a gap between methods and practice (application papers not using methods recommended in papers that were available at the time of the study) or are due primarily to the timing of methodologic theory publication relative to the studies performed. The reasons for gaps between methods and practice are not clear from application papers. Possible explanations include the practitioner being unfamiliar with the published methodology and disagreement on the part of the practitioner on the validity of the proposed methodologies.
The purpose of our review is threefold: 1) to summarize state-of-the-art methodologic approaches; 2) to identify areas where obvious gaps between methodologic theory and practice exist; and 3) to recommend potential areas where theory and methodology may need further development. We recognize that the natural history of disease differs among cancer sites and that attributes of screening tests vary among different screening technologies. While these differences are important, we limit our suggestions to general methodologic areas that may benefit from future research. We look at several key areas in designing screening case-control studies: selection of case and control subjects, definition of exposure, and biases.
In preparing this review, we followed the published methodologic guidelines for review papers ( 2 ) . A comprehensive literature search was performed to identify papers and books on both methodologic theory and application of cancer screening case-control studies published in the English language before January 1997. Sources of information were identified through personal knowledge contributed by the co-authors, conferences, Medline searches, the National Cancer Institute Physicians Database Query (PDQ), and references from published papers and books. Unpublished work was excluded unless it appeared in conference proceedings. Narrative techniques are used to summarize the methodologic theory and application papers reviewed.
We restrict our review to study designs that use mortality from the cancer under study as the end point. For example, we excluded published studies of cervical cancer and prostate cancer screening that use an end point of cancer incidence or advanced disease. The end point of mortality was chosen for simplicity, since it is the most objective end point, and because it is the primary goal of screening. Papers included in this review are listed by publication year in Table 1 . The table is organized into 5-year time periods by year of publication so that methodologic theory and application papers published in the same time frame are easily identified. For the purposes of classification in Table 1 , we list a paper under application if it includes a case-control study with mortality as the study end point.
1. Selection of Case and Control Subjects
As in all case-control studies, the definition of a “case” involves the establishment of a clear, objective study end point and eligibility criteria for individuals included in the study ( 1 ) . Eligibility criteria restrict study participants to those who are at risk for exposure (i.e., have the opportunity to be screened) and are at risk for the study end point (i.e., death from the cancer under study). Case and control subjects are identified from the source population by use of the same eligibility criteria. In the next few sections, we discuss several issues that are of concern in screening case-control studies, including potential source populations for screening studies, special concerns in defining a case, and the selection of control subjects.
A. Source Population
I. Methodologic theory papers. Dubin et al. ( 3 ) stated that a source population must contain both case and control subjects, screening must be available to its members, and identification of individual screening histories of the case and control subjects should be accurate and easily obtainable. One common recommendation for defining a source population is to target a specific geographic area where screening is widely available. However, in populations defined geographically, it may be difficult to identify all cancer deaths and to obtain complete screening records. Another method of defining a source population is to use the members of a health-care plan, as demonstrated by Newcomb et al. ( 4 ) and Selby et al. ( 5 ) in the application of case-control methods. Cohen ( 6 ) suggested the use of population-based administrative databases that include screening information as a possible method of defining source populations and discussed both the advantages and the disadvantages of this approach. He gave an example using the Manitoba, Canada, Cancer Registry.
II. Applications. The source populations used in the application papers reviewed are shown in Table 1 . The source populations fell into categories defined by either geographic location, where screening was available to residents, or membership in a health-care plan. In general, studies that used defined geographic locations did not have detailed medical histories available to differentiate those who came in for routine screening because of the presence of symptoms from those with no symptoms and had limited ability to control for confounders in the analysis. Screening histories were usually obtained through a search of screening center records rather than from complete medical records. When a screening test method was common, such as lung x rays ( 7 ) or Pap smears ( 8 ) , researchers were unable to obtain information on tests performed outside of the screening program. Studies that used membership in a health-care organization to define the source population had additional information from medical record review. In this population, preventive services are covered by the health-care plan, so there is no incentive on the part of the provider to justify payment by suggesting the existence of symptoms when none are present. Although this did not eliminate the problem of identifying symptomatic testing, it did enable researchers to address the issue. Medical record review also gave information on possible confounders, such as related disease or medical procedures and family history.
III. Link between methodologic theory and practice. The source populations used in practice were consistent with methodologic recommendations. Future research opportunities exist in applying the case-control method to other types of populations (such as administrative databases) and exploring the advantages and difficulties unique to each type.
B. Case Selection
I. Methodologic theory papers. The methodology for defining case subjects in a screening case-control study was first addressed by Morrison ( 9 ) who stated that case subjects should be based on a manifestation of disease that develops only after the preclinical stage of disease. Although various manifestations of late stage disease are possible end points and have been used in case-control studies ( 10 ) , mortality, which most objectively meets this requirement, is widely used and is our focus. There are methodologic and interpretive implications to defining a case on the basis of mortality. Exposure information, when it is not available in written records, must be obtained from a proxy. Identifying case subjects from the source population may not be straightforward. This issue was addressed by Weiss ( 11 ) and by Gill and Horwitz ( 12 ) who discussed methods for identifying deaths due to a specific cause. Weiss suggested that looking at death certificates may not be sufficient; medical records should also be reviewed. Gill and Horwitz discussed the potential of comorbidity to interfere with the accurate attribution of death when studying an older population. They suggested blinded case attribution and rigorous methods to determine the cause of death; moreover, the methods used should be reported along with the study results. A second consideration in case definition is the timing of cancer diagnosis relative to the availability of the screening test. Moss ( 13 ) discussed the need to allow for a start-up time at the initiation of a screening program to guarantee that the case subjects and the matched control subjects will have the same access to screening before the case subjects are diagnosed. She cited the example of the breast cancer screening study in Utrecht ( 14 ) , where case subjects were included if they were diagnosed after the start of the screening program, not allowing for the 2-year start-up time during which women were invited for their first screening. In this situation, the case subjects or the matched control subjects may not have been invited to their first screening before the end of the exposure period (i.e., the time of diagnosis for the case subjects). Moss ( 13 ) also reasoned that a truer indication of the long-term effects of screening could be obtained by excluding deaths that occurred soon after the initiation of a screening program, since the benefits of the program would not be expected for several years. Gill and Horwitz ( 12 ) also discussed the issue of adequate follow-up time after the screening enrollment period. Without adequate follow-up time for subjects diagnosed by screening, the study outcome of death from cancer might not be observed.
II. Applications. As required by the inclusion criteria for this review, all application papers defined case subjects as individuals who were diagnosed after screening became available and died within a specified period of time. This time period varied widely both in the elapsed time from the initiation of the screening program to the beginning of the time period during which cancer deaths were counted as possible case subjects and in length. Many studies ( 7 , 8 ,14–23) included deaths that occurred soon (within 5 years) after the initiation of a screening program as cases. All cases were diagnosed after the start of the screening program, but, as Moss points out, this criterion alone does not guarantee that the case subjects had been invited for their first screening tests before being diagnosed. Verbeek et al. ( 16 , 17 ) and Palli et al. ( 19 , 20 ) further restricted case subjects to those who had been diagnosed after their first invitation to screening (for breast cancer). Moss et al. ( 18 ) used time from entry in the study for case and control subjects rather than calendar time to ensure access to screening. Wahrendorf et al. ( 24 ) defined cases (colorectal cancer) as deaths occurring more than 6 years after the introduction of screening to allow enough time for the screening program to be fully implemented and to yield individual protection. All studies identified potential case subjects through some combination of cancer registries and death certificates, with the exception of Wahrendorf et al. ( 24 ) who had to rely on the follow-up of case subjects identified through biopsy specimens. Some of the population-based studies ( 21 , 23 , 25 ) included a review of medical/hospital records to verify the cause of death. The studies performed within a health-care plan used medical chart review to verify the cause of death.
III. Link between methodologic theory and practice. There was an awareness in the application papers of case ascertainment difficulties, and methods for finding case subjects within the source population were reported. The methodologic theory papers were unclear on the appropriate time frame for identifying case subjects. Application papers gave little attention to the potential effects on study results that are related to the initiation phase of a new screening program. In addition, studies did not always explicitly state eligibility criteria that guaranteed that case subjects would have had the opportunity to be screened before diagnosis. Future research is needed to study the effect of the time period for identifying cases, including its initiation relative to the start of a new screening program, and to determine how long after screening becomes available is needed to accurately assess efficacy.
C. Control Subject Selection
I. Methodologic theory papers. In cancer screening case-control studies, case and control subjects are matched on variables that are related to the risk of cancer or the opportunity to be screened, such as age or sex. Typically, control subjects are randomly selected from a source population comprised of nondiseased and diseased, noncase individuals ( 9 , 26 ) . Weiss ( 26 ) noted that exclusive use of diseased control subjects would almost never be appropriate, since such individuals would not be representative of the source population from which case subjects were identified. Sasco et al. ( 10 ) stated that control subjects should also be disease free at the time of diagnosis for the case subjects to ensure that the control subjects were at risk for exposure to the screening test during the defined exposure period. Knox ( 27 ) discussed the potential bias associated with excluding individuals who had been previously diagnosed with cancer, a group that includes individuals that may have benefited from screening. Care must be taken to ensure an equal opportunity of exposure for the case subjects and matched control subjects, particularly during the initiation phase of a screening program when the case subjects may be diagnosed before the control subjects are invited to be screened ( 13 ) .
II. Applications. All application studies reviewed used matched control subjects sampled directly from the source population. In addition, Ebeling and Nischan ( 28 ) (lung cancer) performed a second analysis with a hospital-based control group that included covariate information that was not available for the control group selected from the source population. A few papers stated an inclusion criterion of control subjects being disease free at the time of diagnosis of the case subjects ( 18 , 21 , 29 ) . The matching criteria varied between papers. All studies matched on some measure of age (either year of birth or age within an interval) and sex when appropriate. Studies using members of a health plan also matched on date of entry into the health plan. Many studies based on local screening programs matched on additional variables believed to be related to exposure ( 7 ,19–24, 28 , 30 , 31 ) . Several studies classified as case subjects those individuals diagnosed after the start of the screening program, but this approach does not guarantee that case subjects and matched control subjects had the opportunity to be screened before the case subject was diagnosed. Verbeek et al. ( 16 ) also stated that control subjects were invited women, but it is unclear whether this restricted control subjects to those who were invited before the case subjects were diagnosed. Moss et al. ( 18 ) used time from first invitation to be screened rather than calendar time for eligibility criteria and exposure definition.
III. Link between methodologic theory and practice. While the application papers are generally consistent with the published methodology, possible inconsistencies exist in two areas. First, several studies do not state that they excluded control subjects who were diagnosed with disease before the case subjects were diagnosed. Second, several application papers did not explicitly state eligibility criteria that guaranteed that case and control subjects had the same opportunity to be screened before the cases were diagnosed. It is not clear from the study descriptions in the application papers if these inconsistencies truly exist.
2. Definition of Exposure
When evaluating the efficacy of screening in a case-control study, the exposure of interest is the screening test. Avoiding bias in the classification of case and control subjects as either exposed or unexposed can be surprisingly difficult. The situation is complicated by the fact that the screening test itself can lead to diagnosis of the disease, and, once a diagnosis is made, screening is no longer possible for that person. The exposure must be defined in a way such that both the case subjects and their matched control subjects have similar risk for exposure if the screening test is not efficacious ( 11 ) . In other words, the control and case subjects should have the same screening rate if the screening test has no effect on mortality. Therefore, it is usually recommended that the exposure period end when the case subject is diagnosed.
When defining exposure, a method for separating true screening tests from tests performed due to the presence of symptoms must be determined, and a procedure for quantifying the exposure measure must be established. The procedure involves identifying the time period of risk considered in the study and classifying individuals with a variety of screening histories as either exposed or unexposed. The period of time during which screening tests are counted toward exposure is called the “exposure window.” We discuss the broad topic of exposure definition in the following two sections to examine the issues more closely.
A. Identifying a True Screening Test
I. Methodologic theory papers. By definition, a screening test is performed on asymptomatic individuals. Tests that lead to a diagnosis in the absence of symptoms are screening tests and should be counted as such ( 9 ) . However, failure to exclude symptomatic tests would lead to bias in estimating screening efficacy. One procedure for eliminating diagnostic tests is to exclude all tests for the case and control subjects for a time period before the case subject was diagnosed. Weiss ( 11 ) argued that excluding tests that occurred in a period before the case subject was diagnosed was equivalent to counting only negative screening test results. Furthermore, since negative test results could not lead to a health benefit ( 27 ) , this approach would not be a good candidate for classifying individuals as exposed. Thus, excluding tests for a period of time before diagnosis is not recommended. Identifying tests performed for screening purposes and tests performed for diagnostic purposes may be difficult, even with a medical record review ( 32 ) . Several studies ( 5 , 29 , 33 ) that included a primary-care medical record review could not make a clear distinction and classified tests as asymptomatic, possibly symptomatic, and definitely symptomatic. Gill and Horwitz ( 12 ) and Friedman et al. ( 32 ) discussed this issue in detail. In some situations, tests may be performed for symptoms not directly related to the disease under study. These tests are still capable of detecting cancer, and their exclusion could introduce bias. For example, if case subjects are more likely to have an associated disease (e.g., benign prostatic hyperplasia for prostate cancer), exclusion of symptomatic tests not directly related to the study outcome could overestimate the efficacy of the screening test. Another concern is that individuals may not undergo screening tests when symptomatic tests for a related disease are performed during the exposure period, which again introduces bias into the analysis. Because of the difficulties in deciding whether tests should be counted as exposures, Gill and Horwitz ( 12 ) suggested addressing this uncertainty by presenting a clinical confidence interval rather than a single estimate. These proposed clinical confidence intervals are calculated by varying the criteria for excluding possible diagnostic or follow-up tests, giving a type of sensitivity analysis for the study criteria used to classify symptomatic tests. Gill and Horwitz ( 12 ) also discussed the situation in which several screening tests are available. In this case, concentrating on one specific test and excluding related tests may be too narrow. For example, obtaining one type of screening test may preclude the use of others. The study by Herrinton et al. ( 34 ) on screening for rectal cancer demonstrated the potential problem. They tested the efficacy of digital-rectal screening in the presence of sigmoidoscopy and fecal occult blood testing and concluded that it was possible that controlling for other forms of screening might obscure the benefits of digital-rectal screening. Weiss and Lazovich ( 35 ) presented an approach to case-control studies that collects data from individuals newly diagnosed with cancer. This approach allows medical records to be augmented with interviews and questionnaires, thus obtaining more accurate information on the reasons screening tests were performed.
II. Applications. In practice, it may not always be possible to identify retrospectively which tests were performed in the presence of symptoms, particularly when screening is performed at screening centers. Several studies ( 7 , 8 , 14 , 16 , 18 ,21–23, 28 , 36 ) considered individuals who participated in a routine screening program as having a true screening test, but the study investigators were unable to check further for the existence of symptoms. The screening program analyzed by Saito et al. ( 25 ) (fecal occult blood screening for colorectal cancer) asked participants about symptoms at the time the screening test was performed. Palli et al. ( 19 , 20 ) included a variable called “self referral” in their analysis. Patients classified as “self referral” had been examined at an earlydetection clinic in the year prior to diagnosis. Several papers ( 23 , 24 , 30 , 31 ) excluded screening tests that were performed close to the diagnosis of the case subjects as a way to eliminate symptomatic tests. When study participants were members of a health-care plan, primary-care medical records were reviewed to exclude symptomatic testing ( 4 , 5 , 29 , 33 , 34 ) . This classification was often unclear, and several authors felt that symptomatic tests could be influencing their study results. Lazovich et al. ( 29 ) (fecal occult blood screening for colorectal cancer) also stratified the data according to whether or not the screening test was a home test (which was deemed less likely to be symptomatic testing). They found a nonsignificant reduction in risk for home tests in comparison with office tests. Herrinton et al. ( 34 ) performed a second analysis involving case subjects with tumors that were too remote to be discovered through digital-rectal examinations. Their goal was to uncover possible bias against screening associated with symptomatic testing that could lead to an odds ratio of greater than 1.0 when the screening test was not efficacious. They found an odds ratio of less than 1.0 and concluded that it could be due to either chance or other types of bias. The study by Friedman et al. ( 32 ) demonstrated some of the more subtle problems associated with classifying tests as symptomatic. They found a larger number of symptomatic tests not clearly related to bladder cancer among the case subjects and a larger number of routine screening tests among the control subjects. A possible explanation for these results is that tests performed for symptoms of disease other than the disease under study preclude routine screening tests. Because of the difficulties in determining which tests should be included as exposures, the authors presented a clinical confidence interval as suggested by Gill and Horwitz ( 12 ) . The odds ratio was close to 1.0 when all tests were included in the analysis, and a statistically significant reduced odds ratio of 0.6 (95% confidence interval = 0.4–0.9) was obtained when only routine screening tests were included.
III. Link between methodologic theory and practice. Several studies excluded tests in an interval before the case subjects were diagnosed, which was inconsistent with the methodology recommendations. However, these studies were published before or slightly after the recommendation not to exclude screening tests. We would not classify this as a gap, but rather as representative of an evolving field of research. The inability to distinguish between screening and symptomatic tests severely limits the ability to perform a valid case-control study. Future research is needed to identify information required to classify tests as screening exposures and to understand better how a previous history of related disease influences future screening practices.
B. Quantifying the Exposure Measure
I. Methodologic theory papers. We consider three general categories of exposure: frequency, defined as the number of screening tests in a specified time period before the case subject was diagnosed; recency, defined as the time between case subject diagnosis and the last screening test performed; and, ever/ never screened in a specified period of time before the case subject was diagnosed. The ever/never measure is the recommended exposure for estimating screening efficacy. In addition, the other exposures listed are sometimes used in supplemental analyses.
Berrino et al. ( 37 ) first pointed out the potential biases in using the frequency of screening tests. Since an individual receiving multiple screening tests is necessarily disease free at several points in time, looking at the frequency of the tests as the exposure measure could lead to a healthy screenee bias. Morrison ( 38 ) concluded that healthy screenee bias could be avoided by using an exposure measure of ever/never screened during a specified time period. Weiss ( 11 ) agreed that one should not consider the frequency of screening tests. Friedman and Dubin ( 39 ) demonstrated the healthy screenee bias by performing case-control studies, using frequency as the exposure, with data from the Health Insurance Plan (HIP) randomized trial investigating breast cancer screening. Hosek et al. ( 40 ) used a deterministic model to demonstrate the bias associated with the exposure measure of screening frequency.
When recency is used as the exposure measure, the analysis is stratified by time between the diagnosis of the case subject and the last screening test prior to diagnosis (e.g., 0–1, 1–2, 2–3, . . . years before diagnosis of the case subject). This measure can potentially introduce bias into the analysis for two reasons. First, individuals can only benefit from the result of a positive test ( 27 ) , which is usually obtained in the interval closest to diagnosis. In the context of breast cancer screening studies, Moss ( 13 ) stated that it would be surprising to find a benefit associated with screening tests not in the interval closest to diagnosis, and such a finding may be the result of selection bias. However, this argument may not apply to screening for colorectal cancer, which can involve the treatment of precancerous disease (removal of polyps) that may prevent the development of cancer in the future. Second, when the cutoff point for the interval closest to diagnosis is relatively small, the control subjects may not have had the opportunity to be screened during that short period of time before the case subject was diagnosed.
Defining the relevant time period for the ever/never exposure (i.e., the exposure window) can be particularly complex. Clearly, screening tests that are performed when no disease is present or when disease cannot be detected are not efficacious. Cole and Morrison ( 41 ) discussed the idea of a detectable preclinical period during which disease can be detected through a screening test but is still asymptomatic. Berrino et al. ( 37 ) developed the idea of using the preclinical detectable phase as the exposure window. Screening before or after that period could not change the outcome of the disease. Weiss et al. ( 42 ) further restricted the interval described by Berrino et al. and developed the idea of the detectable, curable preclinical phase. Berrino et al. and Weiss et al. acknowledged that neither of these preclinical phases would be known. Furthermore, these intervals vary according to the individual and the screening test under study. An estimate of the average length could be used or, as suggested by Weiss et al. ( 42 ) , a range of intervals to give a sensitivity analysis associated with the exposure window.
II. Applications. Each application paper reviewed used the ever/never screened measure, and several studies ( 5 , 14 , 19 , 20 , 23 , 25 , 28 ,30–33) used frequency and/or recency as well. The goal of using recency as the exposure measure was not always clear. Selby et al. ( 5 , 33 ) used recency to estimate the number of years from being free of polyps to the development of colorectal cancer, thus defining the appropriate screening interval. Friedman et al. ( 32 ) (bladder cancer) and Pisani et al. ( 23 ) (gastric cancer) used the recency exposure to explore the possibility of bias in their analyses. Most studies used the ever/ never exposure with an exposure window of all screening history up to the date of diagnosis. However, in many studies, screening had only been offered for a short time, so there was an implicit window of exposure that varied depending on when the case subject was diagnosed. A number of studies ( 5 , 7 , 21 ,28–30, 33 , 34 ) reported a range of exposure windows as a sensitivity analysis for the exposure measure. A problem may arise when the recommended screening interval, or screening cycle, is longer than the exposure time considered. For example, Lazovich et al. ( 29 ) analyzed a study population that participates in a health plan that recommends biennial screening for colorectal cancer. When looking at an exposure period of 1 year before the diagnosis of the case subjects, the control subjects had an unexpectedly low screening rate. One possible explanation is that some of the regular biennial screening attendees among the control group may not have had an opportunity to be screened in the year prior to case subject diagnosis. Thus, the opportunity to be screened was different for the control subjects and the case subjects diagnosed by screening, since the interval was defined by the case subjects.
III. Link between methodologic theory and practice. Several studies used frequency as a supplemental exposure measure, which is not recommended in the published methodologies. The largest gap between methodologic theory and practice is found in defining the exposure window. The use of a preclinical detectable phase and a detectable, curable preclinical phase cannot be directly applied, since they will not be known on either an individual or a population level. Future opportunities include both identifying the appropriate exposure window and investigating differences between prevalence and incidence screens and how these differences may be captured in the exposure measure. When using the ever/never measure, the exposure window is defined by the case subjects, usually ending when the case subjects are diagnosed. This approach makes the exposure definition inherently different for the case subjects who were screen detected and their matched control subjects. Research is needed to understand better how this difference affects results from case-control studies. Specifically, potential research opportunities include study of the relationship between the screening cycle and the exposure window and the interplay between the exposure window and case definition as they relate to the opportunity for case and control subjects to be screened.
There are numerous opportunities for the introduction of bias into screening case-control studies, many of which have already been discussed. In the section on case definition, we discussed the bias related to the identification of case subjects within the source population (case ascertainment bias) and by the lack of adequate follow-up time after screening becomes available. In the section on the exposure measure, we discussed the use of screening frequency (healthy screenee bias) and the inability to identify symptomatic tests (information bias). The review of case-control methods for screening studies by Weiss ( 11 ) discussed bias in some detail and included a section on the control of confounding variables.
It is generally believed that individuals who choose to participate in screening programs are different from those who choose not to participate. This is called self-selection bias and has been given a great deal of attention in the screening case-control literature. Therefore, we limit our discussion to self-selection bias.
A. Self-selection Bias
I. Methodologic theory papers. Weiss ( 26 ) stated that comparisons of case and control subjects may be difficult, since the incidence and mortality rates may be different for screened and unscreened groups. He also noted the HIP trial, in which individuals who refused screening had a lower incidence rate than individuals who were in the control group and were not offered screening. Dubin et al. ( 3 ) argued that, since it may not be possible to remove this bias, a study must collect information on known risk factors for the disease. Moss ( 13 ) concluded that it would be dangerous to make statements about screening efficacy based solely on the comparison of screening acceptors and rejecters. She suggested that the case-control methodology may be better suited for the comparison of screening strategies rather than assessing efficacy. Gill and Horwitz ( 12 ) suggested that results should be stratified by risk group rather than adjusting for confounders to obtain an average effect. This approach would provide the opportunity to identify how benefits may vary among risk groups. Connor et al. ( 43 ) , Friedman and Dubin ( 39 ) , and Gullberg et al. ( 44 ) all performed case-control studies using data from randomized trials. Connor et al. and Friedman and Dubin found that individuals in the HIP trial who accepted screening were at higher risk for breast cancer (incidence and mortality) than individuals in the control group. Gullberg et al. performed a case-control study within the randomized trial of screening mammography. They found that those who refused screening were not at a higher risk of incidence but were at a higher risk of mortality than the control group. Gullberg et al. suggested that comparing incidence rates for individuals who refuse screening with the rates for a control group does not give a valid estimate of self-selection bias. Moss et al. ( 18 ) performed a case-control study of breast cancer screening within a larger cohort study. They concluded that those who had refused screening had a poorer prognosis after diagnosis than individuals in the comparison population. It is interesting to note that selfselection bias can vary from one study to another, even when using the same screening test. The bias found by Gullberg et al. and Moss et al. is in the opposite direction of the self-selection bias found by Connor et al. and Friedman and Dubin in the HIP trial.
II. Applications. The application papers reviewed attempted either to match on possible confounders or to collect information on confounder variables to be included in the analysis. In addition, several authors made attempts to assess the amount of self-selection bias present in their study results. Collette et al. ( 14 ) (breast cancer screening) compared the mortality and stage distribution of the unscreened group with the same measures in the general population before screening was introduced and found them to be similar. Verbeek et al. ( 16 ) compared incidence rates and van Dijck et al. ( 36 ) compared mortality rates for breast cancer in the unscreened group with rates for individuals in a neighboring town and found them to be similar. In the study on screening for lung cancer by Ebeling and Nischan ( 28 ) , important covariate information was not available for the control group sampled directly from the source population. Ebeling and Nischan performed a second analysis, using a hospital-based control group with covariate information, and compared smoking rates in screened and unscreened groups. Newcomb et al. ( 4 ) and Selby et al. ( 5 ) performed a second analysis using case subjects with colorectal tumors that could not have been detected by the screening procedure (out of reach of the sigmoidoscope). These analyses gave odds ratios close to 1.0, as would be expected in the absence of selection bias. Herrinton et al. ( 34 ) did a similar analysis with tumors too remote to be discovered by digital-rectal examinations. They found an odds ratio less than 1.0 and suggested that it could be due to self-selection bias. Pisani et al. ( 23 ) felt that self-selection bias was affecting the results of their study of gastric cancer screening and performed a second analysis using only individuals who had been screened at least one time.
III. Link between methodologic theory and practice. Application papers addressed the concerns demonstrated in the methodology papers by either attempting to control for or to test for the existence of self-selection bias in the study populations. The more recent methodology suggestion of stratifying by risk group has yet to be implemented in practice.
It is interesting that methodologic theory and practice are not always closely linked. Two recent examples include the methods and practice of causal inference methodology ( 45 ) and the methods and practice of writing review papers ( 46 ) . In both areas, major discrepancies have been found between methods and practice, discrepancies explained in large part by the fact that practitioners seemed to be unfamiliar with the published methodology. However, for screening case-control studies, there seems to be an awareness of the published methodology by those performing case-control studies in this field. With one exception ( 20 ) , application papers referenced some subset of the methodologic papers available to them at their time of publication. The transfer of ideas from methodology to practice was undoubtedly facilitated by the fact that several individuals work in both areas.
Nevertheless, some discrepancies between methodologic theory and application exist. The largest of these is found in areas where the state-of-the-art methodology cannot be readily implemented in practice, such as estimating the appropriate exposure window for screening tests. In two other areas, the practice of case-control studies did not agree with recommended (and practicable) methodologies: excluding screening tests that occur in a specified time period before the case subject was diagnosed and using screening frequency as an exposure measure. It is likely that Weiss' ( 11 ) paper recommending against excluding tests before diagnosis was published after the analysis of the case-control studies that used this procedure. However, the potential bias associated with frequency of screening tests as a measure of exposure was discussed by Berrino et al. in 1983 and later addressed by Morrison in 1985 and Weiss in 1994. Nonetheless, several application papers calculated an odds ratio based on screening frequency. These studies also used some form of the ever/never exposure measure. Thus, their conclusions were based on a number of exposure measures rather than screening frequency alone. The use of screening frequency did not change the study outcomes.
Although it is good that the application of the case-control approach closely follows current methodologies, many important problems remain. Case ascertainment issues, such as the effects of comorbidity and the timing of cancer deaths relative to when screening became available, are important concerns. The ability to identify screening and diagnostic tests seems crucial in obtaining valid results. The role of related disease and testing needs to be defined clearly. Other areas that need to be examined more carefully include the following: the effects of selection bias; identifying and controlling for confounding factors; incorporating uncertainties in collection and interpretation of screening histories; and, identification of case subjects from the source population.
Case-control studies are increasingly used to assess the efficacy of screening tests and, therefore, may influence policy decisions (i.e., screening recommendations in preventive medical practice and public health). Clinical trials report effectiveness of a screening program rather than efficacy of a screening test, since the analysis in a trial compares those offered screening versus those not offered screening rather than those who have a screening test versus those who did not. Therefore, when screening recommendations are implemented, the efficacy measure will overestimate the effectiveness of the screening program.
Because screening case-control studies are susceptible to many sources of bias, a careful assessment of the practice and theory of the methods is warranted. Given the current state of theory and practice, we believe that, when evaluating the efficacy of a screening test, evidence from case-control studies must be carefully scrutinized. Caution must be taken in both the undertaking of studies and interpretation of study results. Implications of a single case-control study result should be discussed in the context of other research and background knowledge related to the screening test and the cancer under study. Replication of study results in diverse populations is essential for the verification of efficacy estimates.
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Lung cancer in never-smokers: a case–control study in a radon-prone area (Galicia, Spain)
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The aim of the study was to assess the effect of residential radon exposure on the risk of lung cancer in never-smokers and to ascertain if environmental tobacco smoke modifies the effect of residential radon.
We designed a multicentre hospital-based case–control study in a radon-prone area (Galicia, Spain). All participants were never-smokers. Cases had an anatomopathologically confirmed primary lung cancer and controls were recruited from individuals undergoing minor, non-oncological surgery. Residential radon was measured using alpha track detectors.
We included 521 individuals, 192 cases and 329 controls, 21% were males. We observed an odds ratio of 2.42 (95% CI 1.45–4.06) for individuals exposed to ≥200 Bq·m −3 compared with those exposed to <100 Bq·m −3 . Environmental tobacco smoke exposure at home increased lung cancer risk in individuals with radon exposure >200 Bq·m −3 . Individuals exposed to environmental tobacco smoke and to radon concentrations >200 Bq·m −3 had higher lung cancer risk than those exposed to lower radon concentrations and exposed to environmental tobacco smoke.
Residential radon increases lung cancer risk in never-smokers. An association between residential radon exposure and environmental tobacco smoke on the risk of lung cancer might exist.
Residential radon exposure increases risk of lung cancer in never-smokers, ETS exposure may raise radon effect http://ow.ly/xRVte
For editorial comments see page 850.
Lung cancer is currently the leading cause of cancer death worldwide. Tobacco consumption is the most important risk factor for lung cancer; however, between 15–25% of all lung cancer cases occur in never-smokers [ 1 ]. Recent research suggests that lung cancer in never-smokers could be a different disease than lung cancer in smokers, since different molecular pathways are present in never-smokers' lung cancer [ 2 , 3 ]. These patients also have higher survival, a different age of onset and have mainly adenocarcinomas [ 4 , 5 ].
Residential radon exposure is the second risk factor of lung cancer after tobacco consumption and the first risk factor for never-smokers [ 6 ]. Residential radon was declared a human carcinogen in 1987 by the World Health Organization (WHO) and in 1988 by the US Environmental Protection Agency (EPA). The US EPA considers an action level of 148 Bq·m −3 whereas WHO has recently lowered the action level to 100 Bq·m −3 [ 6 , 7 ].
Two pooling studies, which included case–control studies performed in Europe and North America, found a linear relationship between residential radon exposure and lung cancer risk [ 8 , 9 ]. The European pooling included 884 never-smoker cases and 5418 never-smoker controls. In the latter subgroup, there is an excess of relative risk of 10.6% per 100 Bq·m −3 was observed, slightly higher than the risk observed for ex- and current-smokers. In the American pooling study there was no difference between ever- and never-smokers for risk of lung cancer. In both groups the excess of relative risk was 10%. Very few case–control studies [ 10 – 12 ] have been performed that have included never-smokers and the results are conflicting. A recent systematic review [ 13 ] suggests a possible relationship between residential radon exposure and lung cancer in never-smokers and it seems that there is a dose–response pattern.
A problem that appears when assessing the relationship between residential radon and lung cancer is the low variability in radon concentrations, which makes it difficult to assess possible dose–response patterns. Galicia, the study area, has been characterised as a radon-prone region by previous studies [ 14 , 15 ]. Furthermore, Galician population has low mobility compared with other populations, which facilitates the attribution of lung cancer to radon exposure [ 15 ].
Environmental tobacco smoke (ETS) is a risk factor for lung cancer. In 1992, it was recognised as a human carcinogen by the US EPA [ 16 ]. Only one study has suggested that there is a synergism between residential radon and ETS [ 12 ]. This synergism could be explained because radon and tobacco smoke may have a different carcinogenic mechanism, with different mutational patterns for each risk factor [ 17 ].
The aim of the present study is to assess the effect of residential radon exposure on the risk of lung cancer in never-smokers and to ascertain if ETS exposure can modify the effect of residential radon.
- Material and methods
Design and setting
We designed a multicentre hospital-based case–control study in the Northwest of Spain (Galicia and Asturias). All public hospitals in Galicia (n=7) and the most important hospital in Asturias (Hospital Central de Asturias) took part. 95% of the patients in the study population area had universal healthcare coverage. Lung cancer diagnosis and staging was only performed in the hospitals included in the study. The study area comprised of both urban and rural areas, and ∼50% of the population lived in detached houses in the countryside.
Cases and controls were recruited between January 2011 and June 2013. All participants were never-smokers. A never-smoker was defined as: 1) an individual reporting <100 cigarettes in a lifetime or 2) had not smoked for 6 months. To be included, cases had to have an anatomopathologically confirmed lung cancer. Cases and controls had to be aged >30 years with no upper age limit. Individuals with previous cancers were excluded. Cases were identified by pneumologists assigned to the lung cancer rapid-diagnosis pathway at each hospital.
Controls were recruited from ambulatory individuals undergoing minor, non-oncological surgery. The following hospitals provided controls: Santiago de Compostela, Ourense, Vigo and Lugo; the first three hospitals cover geographic areas that have slightly higher residential radon concentrations than the Lugo area. Controls were selected using a frequency sampling on age and sex distribution regarding cases in order to assure comparability between cases and controls on these two variables.
The study protocol was approved by the Galician Committee of Research Ethics (reference 2010/295) and all participants signed written consent for participation.
Data collection and radon measurement
All participants were personally interviewed at hospital by trained researchers using a questionnaire. They were asked about different aspects of their lifestyle, with special emphasis on ETS exposure, leisure time exposures, diet, and alcohol consumption. Participants provided a biological sample of 3 mL of blood in order to analyse genetic polymorphisms and its relation with lung cancer onset.
We retrieved detailed information on ETS exposure from all participants. We asked them if they had or had not lived with a smoker during the last 20 years. In an affirmative case we asked about the relationship, the number of years of cohabitation, and the number of cigarettes per day smoked by the cohabitant. We collected information of up to four smoking cohabitants. We also collected information for ETS exposure during childhood or at work. Since the most relevant exposure for lung cancer appearance is ETS at home and due to changes regarding smoking at work (enforced by law) in the recent years, we only considered ETS exposure at home in our analysis.
The interviewer gave the participants a radon detector to take home and positioning instructions, which included a picture on how to correctly position the detector in the home. Participants also received a prepaid envelope to send back the detector to the coordinating centre once the measurement period had finished. The detector was of the alpha-track type (CR-39; Radosys Inc., Budapest, Hungary). The detector was placed in the participant's bedroom, at a height between 60 and 180 cm from the floor, away from doors, windows, heating and electrical devices. The minimum period of exposure was 3 months. 1 week after the detector was given to the patient, a researcher phoned the participant. This was undertaken in order to ensure the correct positioning of the device and to answer any doubts or questions the participant may have had. Once the exposure period finished, another phone call was made to inform the participant that he/she should send back the radon detector. Specific instructions for sealing the device, once it was retired from use, were given. The devices were read at the Galician Radon Laboratory (Santiago de Compostela, Spain), which has been certified by the University of Cantabria, with excellent results in intercomparison exercises [ 18 ]. We also performed periodical quality controls with blanks and sending detectors to other radon laboratories for intercomparison purposes. Radon measurements were seasonally adjusted in order to consider radon variability throughout the year. We sent to the participants the results of the radon measurements, with specific recommendations depending on the radon concentration observed at each home.
We performed a bivariate descriptive analysis to determine the distribution of the study variables according to the case or control status. Following this analysis, we used a multiple logistic regression where the dependent variable was the case or controls status and the independent variable residential radon exposure broken down in four categories (≤100, 101–147, 148–199 and ≥200 Bq·m −3 ). As adjustment variables, we introduced in the model age (continuous), sex, and ETS exposure defined as having lived with a smoker or not for >20 years. We repeated the same analysis but only including females and also including only individuals who had lived ≥20 years in the same dwelling.
To assess if ETS exposure at home, defined as the time living with a smoker modified the risk of lung cancer due to residential radon, we created a variable with six categories through syntaxes. This variable combined two categories for residential radon (<200 and ≥200 Bq·m −3 ) and three for years living with a smoker (0, 1–35 and ≥36 years). The results were adjusted by age and sex. All the results are expressed as odds ratios with 95% confidence intervals. The software used for the analysis was IBM SPSS v20 (IBM, Armonk, NY, USA).
521 individuals, 192 cases and 329 controls were included. The participation rate was high, >90% of cases and 75% of controls accepted to took part in the study. 15 cases (7.8% of the total included) were recruited in Asturias. The sex distribution was very similar among cases and controls and also the age distribution. 21% were males and the median age was 70 years for cases and controls. Education levels were similar between both groups and the percentage of individuals who had worked in risk occupations for lung cancer did not differ between cases and controls. More cases than controls lived in rural areas, but there were no statistically significant differences between radon concentrations in each of the habitats, though residential radon was slightly higher in rural areas. Radon exposure was considerably higher among cases compared with controls. 48% of cases had residential radon exposure >200 Bq·m −3 compared with 29.4% for the controls. The returning rate of radon detectors was 177 (92.2%) out of 192 for cases and 272 (82.6%) out of 329 for controls. The median number of years living in the measured home was 30 years for cases and 36 years for controls. The percentage of controls living with smokers in adulthood was 45.1% compared with 42.2% in cases (p=0.051). Regarding histological types, 77.5% had adenocarcinoma, followed by 10.0% with squamous cell carcinoma. The sample characteristics appear on table 1 .
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Regarding the effect of residential radon on lung cancer risk in never-smokers, we observed an OR of 2.42 (95% CI 1.45–4.06) for individuals exposed to concentrations >200 Bq·m −3 , taking those individuals exposed to <100 Bq·m −3 as a reference. The other exposure categories did not show a significant effect. When we restricted the analysis to only females, we observed an OR 2.84 (95% CI 1.58–5.09) for those exposed >200 Bq·m −3 . Finally, for individuals who had lived for ≥20 years in the same dwelling, we found 1.83 OR (95% CI 1.01–3.30) when patients were exposed to ≥200 Bq·m −3 compared with those exposed to <100 Bq·m −3 . The effect of radon exposure on lung cancer risk can be observed in table 2 .
The effect modification, due to exposure to ETS, on the relationship between residential radon and lung cancer is shown in table 3 . The risk of lung cancer does not increase with the number of years living with a smoker for individuals exposed to residential radon <200 Bq·m −3 . Nevertheless, for individuals exposed to >200 Bq·m −3 the risk of lung cancer is higher for all categories of ETS exposure when compared with their counterparts exposed to radon levels <200 Bq·m −3 . Individuals exposed to >200 Bq·m −3 and who have not lived with a smoker show a risk of 1.99 (95% CI 1.16–3.41) and this risk changes to 2.75 (95% CI 1.44–5.25) for those who have lived 1–35 years with a smoker. The last category has a nonsignificant OR of 0.63, although there were only seven cases and 20 controls in it.
The results of the present study show that residential radon increases the risk of lung cancer in never-smokers when they are exposed to indoor levels >200 Bq·m −3 . The risk is more than two-fold when compared with those participants exposed to levels <100 Bq·m −3 . The risk is similar for females and for individuals having lived ≥20 years in the same dwelling. Our study is the first to suggest a possible association between residential radon exposure and ETS on the risk of lung cancer.
The present study provides important insights into the health effects of radon exposure in never-smokers, since very few case–control studies have been performed in never-smokers. We observed that the risk becomes significant when levels of radon are >200 Bq·m −3 ; however, the action level as recommended by US EPA is 148 Bq·m −3 and WHO recently recommended the action level as 100 Bq·m −3 [ 6 , 7 ]. The US EPA and WHO recommendations are based on studies that mainly involved ever-smokers [ 8 , 9 ]. There is an interaction between radon and smoking on the risk of lung cancer, additive or submultiplicative [ 8 , 15 , 20 ], therefore, the residential radon concentrations necessary to promote lung cancer in ever-smokers should be lower than in never-smokers. The present results confirm this hypothesis; where a significant risk of lung cancer appears only at high concentrations of residential radon (>200 Bq·m −3 ). This holds true when analysing joint exposure to ETS and indoor radon. In the current study it was decided to use 100, 148 and 200 Bq·m −3 as the cut-off points for radon exposure. 100 Bq·m −3 had to be used as the first category because few individuals were exposed to radon concentrations <50 Bq·m −3 (n=26). However, this first radon level cut-off point is higher than those used in other studies [ 8 , 11 , 12 , 21 – 23 ]. The second cut-off point corresponded to the US EPA action level (148 Bq·m −3 ), and the final cut-off point (200 Bq·m −3 ) is the recommended indoor radon concentration for new houses in the European Union [ 24 ].
Available studies on radon and lung cancer in never-smokers show quite similar results. However, most of them were not designed to assess the risk of lung cancer in never-smokers and only present the results as a subanalysis of the main research [ 8 , 9 , 21 , 23 , 25 , 26, ]. Studies that exclusively involved never-smokers or had a high sample size of never-smokers in the overall sample, observed a linear increase in excess of the relative risk (ERR) with exposure to residential radon of 0.106 (95% CI -0.09–0.42) per 100 Bq·m −3 in the European pooling study [ 8 ] and an ERR of 0.28 (95% CI -0.05–1.05) in the study by L agarde et al. [ 12 ]. The two most important studies performed in never-smokers are the European pooling study [ 8 ] and the study by L agarde et al. [ 12 ]. Both studies have shown a dose–response effect for radon and lung cancer in never-smokers. The European pooling study shows a statistical significant effect from 100 Bq·m −3 (OR 1.23, 95% CI 1.02–1.48) and the risk increases with radon exposure. The study by L agarde et al. [ 12 ] shows a significant effect at 140 Bq·m −3 (OR 1.4, 95% CI 1.0–2.1). These results show that the risk for lung cancer might be evident at <200 Bq·m −3 for never-smokers. A recent systematic review published by our group [ 13 ], concluded that it seems to be a dose–response relationship between residential radon and lung cancer in never-smokers. Nevertheless, the results obtained by the different case–control studies mainly depend on the study setting, with those investigations performed in radon-prone areas tending to obtain significant risks and those in areas with low-dose residential radon showing no effect [ 11 ].
The slightly higher risk of lung cancer observed when only females were analysed could be due to several explanations: hormonal factors, higher exposure to passive smoking than males [ 27 ], or in fact that Galician females spend more time at home than males, since most of the included females were housewives.
An interesting result is the effect modification observed with ETS exposure and residential radon. For individuals exposed to >200 Bq·m −3 the risk of lung cancer increases with the number of years living with a smoker, with the exception of the last category that was composed of individuals who had lived >35 years with a smoker. For this category there were only 27 individuals, seven cases and 20 controls and, therefore, this particular result cannot be considered conclusive. ETS and radon are human lung carcinogens [ 28 , 29 ] and it is biologically plausible an association between both risk factors. Since there is an interaction between radon and active smoking, an interaction between radon and ETS is highly possible. Nevertheless, lung cancer risk entailed by ETS exposure is much lower than that posed by active smoking and, therefore, we would need higher radon concentrations and prolonged periods of ETS exposure to find out if such an association exists. In our case, we divided ETS exposure at home into three categories, taking into account that for active smoking it is the duration of smoking that is more important than the number of cigarettes smoked per day for lung cancer risk [ 30 ]. The possibility of a joint effect could also be supported due to the different carcinogenic mechanisms of ETS substances [ 31 , 32 ] and radon exposure, which is largely unknown [ 17 ]. It is important to highlight that ETS exposure is very difficult to measure. A latency period for lung cancer induction has not been defined and there is no consensus about the best way to measure (and integrate) the effects of ETS exposure than can come from different sources [ 33 ]. Nevertheless, ETS exposure at home is the most relevant exposure for lung cancer.
The present study has been performed in a radon-prone area, which is an important advantage because it allows the assessment of dose–response effect of residential radon. In fact, the high levels of radon in Galicia places the population in a natural experiment [ 34 ]. Previous studies [ 14 , 15 ] have observed that ∼10–12% of Galician dwellings have residential radon levels >200 Bq·m −3 . In the present study 29.4% of the controls had residential radon >200 Bq·m −3 . The difference is probably due to previous studies not including areas of Southern Galicia that have naturally high levels of radon, which we included in the present study. There are two more remarkable advantages. The first advantage was the high rate of radon devices returning from cases and controls, > 90% for cases and 80% for controls. This was due to the thorough follow-up with the participants, mainly through phone calls. To our knowledge, these figures are the highest reported in the literature. The second advantage is the high number of years that the participants have lived at the same home. The median number of years in the measured dwelling was 30 years and 36 years for cases and controls, respectively, and a low percentage lived <20 years. These results are similar to other studies [ 15 , 35 ], facilitating an easier attribution of lung cancer to radon exposure in comparison with other settings. Finally, the multicentre nature of our study increases its external validity and has allowed the achievement of a relatively high sample size, considering that lung cancer in never-smokers is a rather infrequent disease.
Our study also has some limitations. We have not been able to separately analyse the effect of residential radon on males, since the frequency of never-smoking males is low, with only 20% of all cases being male. Other investigation in the same area observed similar results [ 15 ], with 23.4% of males in a large series of never-smoking lung cancer cases. The percentage is also similar (20.7%) in a study performed in Taiwan, with >1500 lung cancer cases [ 16 ]. Regarding ETS there is no standardised measurement for this exposure [ 33 ] and we have chosen as a proxy for this exposure the years living with a smoker in the same home without considering the number of daily cigarettes per day for each inhabitant. Nevertheless, the measurement of ETS is extremely complex, because we should take into account the number of cigarettes smoked in the presence of the participant, the number of days (including or not the days during the weekend) and so on. Recall bias might be present, with cases trying to make a greater effort in remembering past exposures to ETS compared with controls. This information bias could be greater for individuals who have lived for a longer period with a smoker. Our trained interviewers tried to avoid this bias performing standardised interviews. There is a low possibility of a selection bias for the included lung cancer cases and controls. Practically all the population living in the studied area has universal healthcare coverage and, to our knowledge, lung cancer diagnosis is not undertaken outside of the participating hospitals. Since the radon device was given at the time of diagnoses, there is a very low probability of selection bias for cases. Controls were selected at four participating hospitals. Three of these hospitals are placed in areas known to have slightly higher residential radon concentrations and this fact could bias the results towards the null hypothesis (no effect for radon). This has not been the case. When we have analysed the results excluding lung cancer cases from hospitals, with a priori, lower radon concentrations in their catchment area (Asturias, La Coruña, Lugo and Ferrol), the results varied very little (data not shown). These hospitals contributed with 56 cases, accounting for 29% of all cases.
To conclude, residential radon is a risk factor for lung cancer in never-smokers. The risk is apparent for levels >200 Bq·m −3 and is practically the same when we restrict the analysis to females or to individuals who have lived for a minimum of 20 years in the same dwelling. There seems to be a joint effect of residential radon with ETS exposure, with individuals with both exposures having a higher risk of lung cancer. These results support preventive and awareness activities to also be directed to never-smokers, with the objective to reduce their exposure to residential radon. Public health authorities should consider including in their messages the higher risk that is posed by residential radon when ETS is present.
For editorial comments see page 850 .
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Support statement: This paper was funded by a competitive research grant from the Xunta de Galicia: 10CSA208057PR “Risk factors of lung cancer in never smokers: a multicenter case-control study in the Northwest of Spain.”
Conflict of interest: None declared
- Received January 26, 2014.
- Accepted June 4, 2014.
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