1 Slone Epidemiology Center, Boston University School of Public Health, Boston, MA.
2 Department of Epidemiology, Harvard School of Public Health, Boston, MA.
Received for publication October 29, 2002; accepted for publication February 6, 2003.
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ABSTRACT |
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abnormalities; case-control studies; pregnancy
Abbreviations: Abbreviation: CI, confidence interval.
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INTRODUCTION |
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For example, a recent case-control study conducted by our group found an association between the use of folic acid antagonists and the risk of cardiovascular defects (1). Since multivitamins containing folic acid might reduce the risk of cardiovascular defects (24), the findings are biologically plausible. To estimate these associations, the study included 3,870 cases and 8,387 controls recruited over 22 years of surveillance.
It would be highly desirable to identify alternative study designs that would lead to a faster, easier, and less costly assessment of the association between drug use and birth defects, while maintaining or improving validity. We therefore explored the strengths and limitations of two designs infrequently used in birth defects epidemiology: the case-crossover design (5) and the case-time-control design (6). To do so, we compared the validity, efficiency, and ease of conduct of these designs with our traditional case-control study of the association between folic acid antagonist use and cardiovascular defects.
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MATERIALS AND METHODS |
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Outcome definition
Cases consisted of 3,870 infants with one or more anomalies of the cardiovascular system. Infants with coexisting neural tube defects (known to be associated with folic acid), as well as those with defects associated with a syndrome (chromosomal or Mendelian-inherited anomalies, amniotic bands, caudal regression, or twin disruption), were excluded (1).
Exposure assessment and definition
Trained study nurses who were unaware of the hypothesis interviewed the mothers of study infants within 6 months of delivery. The interview included questions on demographic characteristics, the mothers medical and obstetric history, the parents habits and occupations, and a detailed history of the use of medications (prescription and over the counter, including vitamins and minerals) from 2 months before conception through the entire pregnancy.
Because most cardiovascular anomalies develop during the second and third months after the last menstrual period (8), mothers were considered exposed if they reported having used folic acid antagonists any time during these 2 months. We assumed no carry-over effect when the drugs were used before this period. We considered as folic acid antagonists drugs known to inhibit the enzyme dihydrofolate reductase (e.g., methotrexate, sulfasalazine, pyrimethamine, triamterene, and trimethoprim) and those that might affect other enzymes in folate metabolism, impair folate absorption, and/or increase folate destruction (e.g., carbamazepine, phenytoin, primidone, and phenobarbital).
Study designs
Ideally, a cohort study would follow a population of pregnant women from conception, ascertain their drug exposure during pregnancy, and then compare the frequency of cardiovascular defects between the offspring of exposed and unexposed mothers. The comparison could be carried out through the computation of the risk ratio of cardiovascular defects. (We will assume for now that the outcome is ascertained in all conceptuses (9).) However, it is important to distinguish the time during which the fetus is at risk of cardiovascular defects (around the second and third lunar months) from the time one has to follow the woman in order to identify the defects (frequently through the end of pregnancy). In theory, the risks in the numerator and denominator of the risk ratio should correspond to the "at risk" period only, because earlier or subsequent person-time is "immortal" (10) (i.e., no structural birth defect develops before or after organogenesis).
In practice, the timing of exposure is usually measured with a precision of only a few weeks. Because of this imprecision and the uncertainty about the exact onset date of the outcome, every mother/conceptus pair will be considered either exposed or unexposed during the whole "at risk" period (i.e., the 2 person-months of follow-up they contribute to the study). Thus, the estimated risk ratio and rate ratio would be identical, and we will not distinguish between them in the following discussion.
Case-control design
In the case-control design, a random sample of women who had an infant with a cardiovascular defect, the case subjects, provides an estimate of the exposure distribution in all the cases in the cohort, and a random sample of women who had an infant without a cardiovascular defect, the control subjects, provides an estimate of the frequency of exposure in all the noncases in the cohort. Both cases and controls provide an estimate of the exposure distribution during the same window of time (second and third lunar months in our study); that is, the case-control design is based on time-matched sampling when applied to birth defects research. Exposure frequencies from cases and controls are then compared through an odds ratio (figure 1). In the absence of selection and recall biases, the odds ratio from the case-control design would be equal to the odds ratio from the underlying cohort, except for sampling variability. For rare outcomes such as birth defects, the odds ratio is approximately equal to the risk ratio (11).
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The designs presented below are slightly different strategies to obtain a control group that will provide an estimate of the expected frequency of exposure for the cases under the null hypothesis of no effect of the exposure. In all these designs, study cases are a sample of the cases in the cohort.
Case-crossover design
This design includes only cases. No control subjects are required. Each case contributes one case window and one or more control windows. The case window is defined as the "at risk" period preceding the event (the second and third lunar months in our example). The control windows are periods of the same length as, and not overlapping with, the case window that provide an estimate of the expected frequency of exposure for each case. The case window and the control windows derive from the same person at different times; that is, the case-crossover design is based on subject-matched sampling (5). Exposure frequencies from case windows and control windows are then compared through a matched (on subject) odds ratio (figure 1).
We used the 2 months preceding the last menstrual period as the primary control window, thus leaving a gap (washout period) of 1 month between the case window and the control window. To explore the sensitivity of the results to the choice of control window, we conducted separate analyses using two additional periods, of 2 months each, as secondary control windows: a period of 2 months preceding the case window (1 month before and 1 month after the last menstrual period) and the fourth and fifth months after the last menstrual period.
It should be noted that all control windows lie outside the period during which a subject in the underlying cohort was considered to be at risk (i.e., second and third gestational months). In the absence of changes in exposure frequency, control windows may be sampled outside the period during which the subjects would be considered at risk in the underlying cohort (i.e., proxy controls) (13). This is similar to selecting nonpregnant women as controls for the case-control design.
Exposed case-crossover
The case-crossover odds ratio can be estimated by the ratio of the number of cases exposed only during the case window to the number of cases exposed only during the control window (i.e., ratio of discordant pairs). Because only discordant pairs contribute to the estimation of the odds ratio in matched analyses, we would obtain the same estimates by including only the cases exposed at least once during the study. We refer to this design as exposed case-crossover. To emulate this design, we used only mothers of case infants in our case-control surveillance study who had used the drugs of interest anytime from 2 months before the last menstrual period to the end of pregnancy. We then compared case windows and control windows of exposure within case subjects as in the case-crossover design.
Case-time-control design
This design includes both cases and controls (as defined for the case-control design). Each of them is considered twice, once for the case window and once for the control window (as defined for the case-crossover design) (6). Within each case subject, exposure frequencies from the case window and the control windows are then compared through a matched odds ratio, as in the case-crossover design. Among control subjects, the frequencies of exposure during the case window and the control windows are an estimate of the exposure distribution in the underlying cohort during two different periods of time, and therefore the matched odds ratio between windows measures the time trend in exposure (on the odds ratio scale) (figure 1) (6).
The case-time-control design, developed to remove the bias in the case-crossover design due to time trends in exposure, is based on two main assumptions: 1) the case-crossover odds ratio is the product of an odds ratio due to the causal effect of the exposure on the outcome and an odds ratio due to the time trend in exposure prevalence, and 2) the latter is the same among cases and controls. Thus, the case-time-control odds ratio is the case-crossover odds ratio (from the cases) divided by the time trend odds ratio (from the controls).
Statistical analyses
For the case-control design, we used unconditional logistic regression to estimate odds ratios and 95 percent confidence intervals of cardiovascular defects in relation to folic acid antagonist exposure. To adjust for confounding, we included the interview year, geographic region, maternal diabetes mellitus, age, multivitamin supplementation, and urinary tract infections in the model. Because we were interested in the acute effects of exposure during a particular period, we also adjusted for previous use of folic acid antagonists.
For the case-crossover and case-time-control designs, we used conditional logistic regression to estimate matched odds ratios and 95 percent confidence intervals (5, 6). To adjust for characteristics that change over gestational time (time-dependent confounders), we included multivitamin supplementation and urinary tract infections in the model.
We used the standard error of the odds ratio to compare the efficiency of these designs. For comparison purposes, in a separate analysis, we randomly restricted the number of control subjects to one per case subject for the case-control and case-time-control designs.
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RESULTS |
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A comparison of the efficiency of these designs is presented in table 3. Despite including fewer subjects, the case-crossover and exposed case-crossover designs had standard errors similar to that of the case-control design with one control per case. Standard errors were larger for the case-time-control design.
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DISCUSSION |
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The case-control design permits study of a wide range of exposures and outcomes, including chronic exposures and gradual outcomes. The case-crossover and case-time-control designs are appropriate only to evaluate transient exposures with immediate and transient effects in relation to abrupt outcomes (abrupt outcomes being defined as outcomes with a short sensitive time period) (13). Although some drugs are given for acute illnesses (e.g., a 7-day course of trimethoprim for urinary tract infection), others are given for chronic conditions (e.g., carbamazepine for epilepsy). The latter cannot be evaluated by these designs because of lack of variations in exposure between case windows and control windows. Birth defects can be considered abrupt outcomes by defining the case window as the period of potential excess risk around the embryologically sensitive period for the specific birth defect. Although the short period of vulnerability for a birth defect may qualify as "abrupt," these designs would be difficult to apply to conditions such as low birth weight, where the sensitive period may last through most of gestation.
The case-control design can deal with time trends of exposure. An inherent assumption in the case-crossover design (and in the exposed case-crossover design) is a constant subject-specific exposure distribution. This condition can be particularly troublesome for drug-safety studies during pregnancy, given the gestational time trends in drug use. The use of many drugs decreases after conception, which may bias estimates toward a negative association when the control windows precede the case window. In our study, the case-crossover odds ratio for folic acid antagonist use was most likely an underestimate, because folic acid antagonist use decreased between the primary control window and the case window. Moreover, the three control windows considered in our case-crossover analysis led to different estimates (odds ratios of 1.0, 0.7, and 2.8); changes in time trends, together with chance, might explain the differences. The bias would go in the opposite direction for drugs with pregnancy-related indications (e.g., nausea or vomiting) or drugs thought to be safe for the fetus (e.g., amoxicillin), where use in pregnancy might increase relative to prepregnancy. A bidirectional sampling of control windows (i.e., before and after the case window) would eliminate part of the bias from exposure gestational time trends were the trends monotonic (13, 14). However, if the outcome (e.g., prenatal diagnosis of a birth defect) affects subsequent exposure, then control time periods should precede the case window. The case-time-control design was developed to remove the bias due to time trends, and the case-time-control estimate (odds ratio = 2.9) might have removed the effects of time trends from the case-crossover estimate. This design assumes that the reduction in folic acid antagonist use is equal among cases and controls (in the odds ratio scale) under the null hypothesis. However, this assumption might not always hold in practice (15, 16).
While the case-crossover design avoids the difficulties of selecting a valid group of control subjects (11), one still must define a control window, which may be troublesome because there may be induction periods and carry-over effects. Leaving a washout gap between the control window and the case window might avoid potential carry-over effects and will decrease the number of cases whose exposure bridged periods (and therefore do not contribute information). However, the time trends of use and differential recall between windows might pose problems if the control window were substantially farther back in time than the case window.
All the designs might be affected by nondifferential misclassification of the exposure. In fact, under certain circumstances, matched studies can be more sensitive to misclassification than unmatched ones (17). However, differential recall may vary with each design. The case-crossover design, unlike the case-control and the case-time-control designs, avoids differential recall between mothers of cases and mothers of controls (5), but within person recall of exposures may be different across study periods; for example, mothers may be particularly aware of exposures during the first months of pregnancy. On the other hand, the case-time-control design would remove the bias due to trends in recall between the case window and the control windows within subjects only if the relative accuracy between windows (in a multiplicative odds ratio scale) were equal for cases and controls (15).
Designs that use each case as her or his own control (i.e., case-crossover and case-time-control) eliminate between-person confounding (due to factors that vary among persons) (5). In pregnancy-related studies, characteristics such as socioeconomic status, maternal age at conception, prior medical or family history, and unknown and/or unmeasured factors that stay constant through pregnancy will also be controlled by this design. In contrast, within-person confounding (due to transient factors correlated in time with the exposure that vary over time within an individual) would not be automatically controlled by these designs. In our case-control study, adjusting for measured potential confounders (both constant and transient) did not materially affect the odds ratio estimates. Self-matched designs would have greater value in situations where unmeasured between-person confounding is a major concern.
Compared with a case-control design, the case-crossover design may reduce the complexity and cost of conducting the study because no control subjects are required (13). Furthermore, using more than one control period per case window or, even better, using the entire case history to estimate the "usual frequency" would increase the precision of the estimates (at no cost if data have already been collected) (18). However, the self-matching used in this approach can decrease precision if the number of concordant pairs is high (i.e., the exposure is long lasting and bridges periods) (11). The case-time-control design uses the same subjects as would a conventional case-control study, so cost and complexity reductions are not advantages of this design and neither is increase in precision. In our example, estimates from this design had wider 95 percent confidence intervals than those from the case-control design.
The exposed case-crossover design is subject to the same limitations and advantages as the case-crossover design but, in certain settings, it may offer a faster answer at less cost. For example, when only series of exposed cases are available (e.g., Food and Drug Administration case reports, clinical series, or cohorts of exposed women identified by teratology information services), one could study the effect of the exposure, but only under the critical assumption that the timing of exposure did not affect reporting.
In conclusion, our example suggests that only in certain limited settings would innovative designs be advantageous over the case-control design in birth defects research. In the absence of time trends of exposure during pregnancy, the case-crossover design might reduce biases while decreasing the costs and difficulties for patients and investigators. Under the critical assumptions concerning the time trends of exposure among cases and controls, the case-time-control design might reduce between-person confounding but it is unlikely to be more efficient than a case-control design. When one cannot be confident of whether the underlying assumptions about exposure can be met, the conventional case-control design may be the safest design.
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ACKNOWLEDGMENTS |
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The authors thank Dr. Malcolm Maclure for his inspiring talk at the 17th International Conference on Pharmacoepidemiology in 2001 and for his encouraging words in private conversation. They also thank Dr. Murrey A. Mittleman for his comments and Dawn Jacobs, Rachel Wilson, Fiona Rice, Rita Krolak, Sally Perkins, Mary Krieger, Kathleen Sheehan, Karen Bennett Mark, Deborah Kasindorf, Clare Coughlin, Joan Shander, Diane Gallagher, Valerie Hillis, Thomas Kelley, and Nastia Dynkin for their assistance. Finally, the authors are indebted to the medical and nursing staffs at each participating hospital; a list of these hospitals is available from the authors.
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NOTES |
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REFERENCES |
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