From the Joint Departments of Epidemiology and Biostatistics and of Occupational Health, Faculty of Medicine, McGill University, Montréal, Québec, Canada.
Received for publication May 14, 2002; accepted for publication July 25, 2002.
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ABSTRACT |
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bias (epidemiology); case-control studies; child; epidemiologic methods; leukemia; selection bias
Abbreviations: Abbreviation: ICD-9, International Classification of Diseases, Ninth Revision.
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INTRODUCTION |
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A concern with population controls is the potential for their recall accuracy not being comparable with that of cases, especially when the disease affecting cases is severe. On the other hand, diseased controls, especially those affected with a severe disease, could achieve a recall more comparable with that of cases. In addition, it could be easier to obtain genetic or other biologic material from diseased controls, especially if they are children. However, there are only limited data specifically comparing inferences that could be drawn in a case-control study using different control groups, either in adults (3) or in children (4, 5).
The objective of the present study is to empirically determine if inferences drawn from a comparison of cases with population controls would be different from those drawn using diseased controls.
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MATERIALS AND METHODS |
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A second control group was recruited. It consisted of age-, sex-, and hospital-matched children diagnosed at the same center as the case. They were chosen if they had a severe disease treated in the same hematology/oncology services as the cases. The eligible diagnoses were cancers other than acute lymphoblastic leukemia and blood-related diseases (such as severe purpura, blood coagulation problems, and so on). A list of all eligible hospital separation diagnoses was provided by the provincial government as well as by each hospital. All medical records were individually checked to determine the diagnosis, the date of diagnosis, and the age of the patient at diagnosis. The closest subject to the case with respect to date of birth and date of diagnosis was the first chosen from the list of eligible patients. A total of 95 controls had severe blood diseases (International Classification of Diseases, Ninth Revision (ICD-9), codes 283289), and 395 had any one of 70 types of primary cancers with the exclusion of acute lymphoblastic leukemia. The response rate in this group was 94.8 percent; 490 hospital controls were recruited.
Approval for the project was obtained from the research ethics committee of each participating hospital and from the "Commission dAccès à lInformation du Québec"; an informed consent was signed by the parents.
Data collection
Trained interviewers administered a structured questionnaire by telephone. A first questionnaire included information on studied exposures and potential confounding factors. Mothers answered questions about their child and about themselves; fathers answered questions about themselves. Among cases, 98.9 percent of mothers answered the mother-child questionnaires, whereas these numbers were 98.6 percent and 97.4 percent among hospital and population controls, respectively. Among fathers of cases, 83.5 percent answered for themselves, whereas 84.5 percent and 80.7 percent, respectively, did so among hospital and population controls. In addition, a general occupational questionnaire was administered, often complemented by a more probing job-specific questionnaire (7) for jobs frequently held by men or women and with a known potential for multiple chemical exposures. Exposure data were coded according to the expert method (8) by experienced chemists blind to the status of study subjects.
Measures
In this report, we chose to analyze two groups of variables: 1) possible risk factors for acute lymphoblastic leukemia (9) about most of which we have previously reported analyses comparing cases with population controls (6, 1013) and 2) factors that we will call random, because at this time we know of no data showing convincing associations with acute lymphoblastic leukemia. Among possible risk factors, most were measured directly in the parental interview. Others relate to occupational exposures as coded by chemists. For the mother, we used radiographs (yes/no) during the year prior to pregnancy, smoking (yes/no) during the first pregnancy trimester, breastfeeding (yes/no), alcohol consumption (yes/no) at any time from 1 month prior to pregnancy to the breastfeeding period, and exposure to herbicides (yes/no) in and around the home during pregnancy. For the child, we used the number of postnatal radiographs (one and two or more) and exposure to herbicides (yes/no) in and around the home. For the father, we used smoking and alcohol consumption (both coded as yes/no) during the month prior to pregnancy. For both the mother and the father, we used occupational exposure to solvents and to polycyclic aromatic hydrocarbons. For the mother, this was exposure (yes/no) at any time in the 2 years prior to pregnancy up to the end of pregnancy and, for the father, the target period was 3 months prior to pregnancy. The random factors that we chose to analyze were the following: cesarean section for the index child, maternal and paternal asthma, and child tonsillectomy prior to diagnosis.
Statistical analysis
First, hospital and population controls were compared using odds ratios and 95 percent confidence intervals estimated from conditional logistic regression; matching factors were age and sex. We carried out analyses controlling in addition for maternal age and level of schooling. However, the changes in the odds ratios with additional adjustment were negligible, so we report the analyses accounting only for the matching factors. Since we started the study, some associations have been reported with a few of the diagnoses affecting hospital controls (9), although at this time none is truly considered causal. Nevertheless, we repeated these analyses after excluding children with brain cancer (ICD-9 codes 191.0191.9), with neuroblastoma (ICD-9 code 194), and with renal and other urinary organs tumors mostly including Wilms tumor (ICD-9 codes 189.0189.9). There were 119 children in the first group, 44 in the second, and 65 in the latter. The comparison then involved a subgroup of 262 hospital controls with 491 population controls. Unconditional logistic regression was used, adjusting for childs age and gender.
To determine if inferences drawn from using hospital or population control groups would be different, we compared the case group with the entire set of hospital controls, the previously described subgroup of hospital controls, and the population controls. Conditional logistic regression was used for the comparison of cases with the entire sets of hospital or population controls. Unconditional logistic regression was used to compare cases with the subgroup of controls adjusting for childs age and sex. Additional control factors were used in both analyses. There was no material difference between the analyses adjusting or not adjusting for maternal age and level of schooling, so the latter results are reported.
For the sake of simplicity in presenting table results, we used only a yes/no comparison for all quantitative factors except for childs radiographs. However, to determine if reporting differed according to categories of exposure, we also analyzed results for maternal smoking and occupational exposures using more than two categories and average duration of breastfeeding in weeks.
The delay between the date of diagnosis (or date of reference for controls) and the interview could influence reporting. However, the age of the study subjects and the calendar period for reporting also need to be considered, as they may be related to the prevalence of risk factors. We addressed this issue by limiting the comparisons to cases and controls accrued between 1990 and 1993 and who were less than 4 years of age at entry. We compared reporting if the delay was less than 2 years (n = 110) or 2 years or more (n = 92). This cutoff point was chosen because it was close to the average delay for each of the compared groups. The delays were 693 days for hospital controls, 710 days for population controls, and 708 days for cases.
Finally, we compared the reported prevalence for certain factors in the two control groups with that from the ongoing probabilistic population surveys carried out in the province of Québec ("Enquête Santé-Québec"). Data were available on smoking and alcohol consumption from a survey carried out in 1987 (14). For the oldest cases diagnosed in 1990 at the age of 9 years and included in our study, the pregnancy period was in 1980. However, most cases were diagnosed at the age of 4 years, and the pregnancy period for them was in 1985, which is close to the date of the population survey used here. We thus limited our comparisons with population data to cases and controls of all ages (09 years) entering the study from 1990 to 1993.
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RESULTS |
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After comparing results according to interview delay, we did not find that prevalences were systematically higher or lower for any of the factors in any of the groups (data not shown). The smoking prevalences for fathers aged 2044 years of age in this study were 41.5 percent and 41.8 percent among hospital controls and population controls, respectively, and 44.6 percent in men of the same age in the general population (14). These numbers were 38.9 percent, 35.3 percent, and 41.5 percent, respectively, for women. Any alcohol consumption in the same age group was reported by 84.7 percent of the fathers of hospital controls and by 80.4 percent among population controls; the population prevalence was 78 percent (14). For women, these numbers were 58.3 percent, 69.9 percent, and 57 percent, respectively (data not shown).
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DISCUSSION |
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Some observations about the reporting of hospital controls versus that of population controls are worth underscoring: The first is that hospital controls tend to report more exposures than population controls do. However, they did not show predictable or "socially desirable" reporting patterns. For instance, fewer mothers of hospital controls reported drinking, but fewer also reported breastfeeding. On the other hand, slightly more reported smoking. Another useful observation is that, for a given factor, mothers and fathers did not report similarly: Whereas an insignificant excess of radiographs was reported by mothers of hospital controls, substantially more fathers of hospital controls reported them; whereas fewer mothers of hospital controls reported alcohol consumption, more of their fathers did; whereas slightly more mothers of hospital controls reported smoking, fewer of their fathers did. These observations suggest that there does not seem to exist a systematic bias in reporting among hospital controls. Occupational exposures were coded by chemists on the basis of job title, the nature and specificity of the industry, and the description of the work environment. The fact that results for these factors were not substantially different from the others is additional evidence supporting the low probability of systematic bias in reporting on the part of hospital controls. Recall also that secular trends cannot explain differences in reporting, as cases and controls were of the same age in the same calendar year.
Excluding control subjects with brain cancer, neuroblastoma, and Wilms tumor changed only one conclusion (that related to tonsillectomy) in comparison with conclusions reached using the entire group. Although there have been reports associating Wilms tumor, brain cancer, and neuroblastoma with exposure to pesticides (15) and to parental occupational solvents (16, 17), in this study, the relation did not seem to be strong enough to change the conclusions that had been reached with the entire group of hospital controls. This suggests that only those diseases that have been clearly and strongly related to the risk factors under study disqualify for inclusion in a control group; alternatively, it also suggests that a diverse group of control diseases can be used even if associations not yet considered causal have been reported for the studied risk factors with some of the diseases included.
Valid controls are those whose exposures are representative of the base. It is reasonable to assume that our method of choosing population controls provided a priori valid controls. We base this observation on the fact that the source of data for controls provided the best current and up-to-date census available for children legally residing in our area. Comparing the reported prevalence for certain factors from this group with the prevalence from population surveys is an additional way of confirming the assumption of validity. It is more difficult to claim that hospital controls are a priori valid based on our method of selection; comparisons of reported prevalences with the general population can help determine that. Assuming limited and imperfect comparisons (differences in calendar periods and in survey questions) and sampling variability, we find that both control groups report prevalences quite compatible with those found in the base. Nevertheless, the comparisons between cases and each control group did not lead to entirely similar results. The use of hospital controls in comparison with population controls apparently created some bias toward the null.
Lieff et al. (4) compared cases of cleft lip and palate with a large group of controls (over 8,000) chosen from infants with other malformations. The exposure of interest was maternal smoking during pregnancy. They compared cases with all controls and with a series of restricted control groups excluding defects that had been reported associated with maternal smoking and found no differences. There were no population controls in this study.
In conclusion, despite small reported prevalence differences between hospital and population controls for possible acute lymphoblastic leukemia risk factors, and with socioeconomic as well as some external data suggesting that study subjects came from the same base population, we observed a certain degree of bias toward the null when using hospital controls in comparison with population controls. Hospital controls did not answer in predictable ways with respect to social desirability, and mothers and fathers answered differently for the same factor, suggesting that there was no systematic reporting bias between them. However, it remains unclear why hospital controls with diseases not known to be associated with the studied factors report more closely to cases than to population controls. This study cannot determine with any certainty which type of control is best because, to achieve that, validation of reporting would be necessary. We did such an analysis for some factors measured in the present study (distance of home to power lines and prenatal radiographic examinations) (5). We showed that there was similar underreporting in all three comparison groups except when publicity in a community targeted a specific factor (in our case the role of power lines), which resulted in overreporting among cases in that community. However, for many risk factors, validation is next to impossible. Despite the importance of the question for epidemiology addressed by this study, there are remarkably few data available.
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ACKNOWLEDGMENTS |
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The author thanks Drs. D. Amre, M. Guiguet, and J. Attia for their comments on a previous version of the paper.
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NOTES |
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REFERENCES |
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