Knowledge of an etiology of a disease is a first step towards being able to prevent some cases of that disease. Alternatively, this knowledge may be useful in targeting persons at high risk with efforts to detect the disease at an early stage. However, achieving these goals may require, not only an understanding of the presence and magnitude of an association of the disease in question with a given exposure, but also having the answers to one or more of the following questions: How soon can disease result after the exposure has first been incurred? To what extent does the size of the altered risk depend on the duration of exposure? Once the exposure has ceased, does the alteration in risk disappear? If so, how quickly?
For example, while postmenopausal women who receive oral estrogen therapy for an extended duration (e.g., >5 years) probably have some increase in the risk of breast cancer, shorter-term use appears not to be associated with an increase in risk (Collaborative Group on Hormonal Factors in Breast Cancer, 1997). When weighing the risks against the benefits of hormone use of less than five years’ duration, these data suggest that an altered incidence of breast cancer need not be considered. As another example, it is commonly recommended that postmenopausal women with an intact uterus who take estrogens unopposed by a progestogen, and who therefore are at a substantially increased risk of endometrial cancer, be regularly screened (by means of vaginal ultrasound or endometrial biopsy) for the presence of endometrial cancer. Once a woman has stopped taking these hormones, can the screening stop as well? If not immediately, then when? The answers to these questions would be based heavily on the results of studies that documented the incidence of endometrial cancer in women who have discontinued estrogens. (These show a decline in risk relative to continuing users, but are divided as to whether the risk ultimately returns to that of a postmenopausal woman who never used hormones (Cook et al., 2006)). Finally, it is recommended that hepatitis A immune globulin be given within two weeks to persons following exposure to hepatitis A infection, but not thereafter, as a means of reducing the risk of later contracting clinical hepatitis (Krugman et al., 1960). Apparently, the time course of the progression of infection to disease is such that, unless given relatively early, this therapy has little or no efficacy.
An important goal of epidemiologic studies is to provide information that bears on disease prevention. Therefore, persons conducting epidemiologic studies that deal with exposures that vary over time must consider, in both their design and their analysis, the likely temporal relationship between exposure and disease occurrence. Studies of aspirin use in relation to the incidence of acute myocardial infarction have focused on the initial hours to weeks after the most recent dose was taken, since aspirin could have a relatively transient influence by means of its anticoagulant properties. In contrast, studies of aspirin use in relation to the incidence of colon cancer typically concern themselves with long-term use and/or use years earlier, given the long preclinical duration of most colon tumors and of the polyps from which many of these tumors arise.
Example 17-1. In the Physicians Health Study, 22,071 U.S. physicians were assigned at random to receive aspirin, 325 mg. every other day, or a placebo for a period of five years (Gann et al., 1993). A reduction in the incidence of myocardial infarction among the group assigned to aspirin led to the termination of the study at that time. Because a number of earlier non-randomized studies had observed a reduced risk of colorectal cancer associated with long-term aspirin use, an analysis of the accumulated data was done for colorectal cancer as well. No difference was found between members of the aspirin and placebo groups for this outcome, either through the five years of the trial (relative risk = 1.15, 95% confidence interval = 0.8–1.7) or during an additional seven years of follow-up (Sturmer et al., 1998). It is possible that truly no association is present between aspirin use and colorectal cancer, that the earlier observational studies were flawed in some way, and that a randomized study was needed to obtain an unbiased result. However, it seems more likely that 5–12 years is too short a period to determine the effect of aspirin on the incidence of this disease; even a substantial decrease in risk might not start to be evident until well over than a decade from the onset of regular aspirin use. Indeed, the authors of the physicians’ study concluded that “prevention trials with longer follow-up of randomized participants” were needed (Gann et al., 1993).
Some illnesses have features that signal a period of time during which the etiologic agent(s) must have been acting. Bunin et al. (1989) exploited this phenomenon in their case-control study of environmental exposures in relation to the development of retinoblastoma. First, they excluded children in whom the disease had already occurred in a first or second-degree relative, since (for this disease) no further non genetic basis for its occurrence need be considered. They further divided the remaining cases into two groups:
1. Children with a constitutional deletion on chromosome 13q (i.e., a deletion present in all cells of the body) and those with bilateral disease (in whom a constitutional genetic abnormality is believed to be present in every case.)
2. Children with unilateral disease and no constitutional chromosome 13q deletion.
In the first group of cases and their controls, interviews with parents focused on exposures that took place prior to conception (e.g., gonadal irradiation), since only exposures prior to conception could have given rise to the genetic abnormality that predisposed to retinoblastoma in these cases. In contrast, parents of cases in the second group and parents of their controls were queried about exposures that took place after conception (e.g., multivitamin use during pregnancy), since earlier exposures were unlikely to have played an etiologic role.
Failure to take into account the relevant period of time during which an exposure is capable of causing disease can dull the ability of an epidemiologic study to document an exposure–disease association. For example, Hertz-Picciotto et al. (1996) have illustrated how the influence of exposures that act during only a part of pregnancy to give rise to adverse outcomes can be underestimated in non-randomized studies if data on their presence are not collected and analyzed during the appropriate window of time during the pregnancy. Considerations of temporality can be important when planning a randomized study as well:
Example 17-2. In order to test the hypothesis that replacement of dairy fat with vegetable fat in the diet can lead to a lower incidence of coronary heart disease, changes were made in the kitchen of one of two Finnish hospitals providing long-term care for patients with mental illness (Miettinen et al., 1983). The incidence of coronary disease among patients 44–64 years was monitored for a six-year period, after which the policies of the two kitchens were reversed—the one that had switched to vegetable fats reverted to dairy fats, while the other now began to use vegetable fats—and the residents of the two hospitals were observed for another six years. About one-third of the residents of each institution during the first follow-up period also were residents of that institution during the second, and so would have had a diet that, during different periods of time, would have been high in dairy fat or in vegetable fat. Since the influence of diet on the incidence of coronary heart disease is not likely to be immediate—the arteriosclerotic changes that diet may modify take time to develop—the authors’ primary comparison of incidence rates before and after the dietary change at the six-year point within each hospital probably substantially underestimates the true size of the association between type of dietary fat and the incidence of coronary heart disease.
Induction and Latent Periods
For etiologic exposures of brief duration, such as eating food contaminated with the hepatitis A virus, or being subjected to a single, intense dose of ionizing radiation, the induction period in a given ill person is the interval between receipt of the exposure and the first presence of the disease. (When the exposure in question is an infectious agent, an alternative term—the incubation period—is also commonly used.) The time between the disease’s first presence and its recognition is the latent period. Since the first presence of disease can almost never be observed, what is measured in specific individuals is the sum of the induction and latent periods (Rothman, 1981). Most epidemiologists, being economical (or lazy!) with language, simply refer to this sum either as the induction or as the latent period. We will refer to it, clumsily, as the induction/latent period.
The distribution of the length of time required for an exposure to give rise to disease can be estimated by examining the relative risk associated with that exposure over successive periods of time after it was sustained. Fig. 17.1 depicts the risk of leukemia and other forms of cancer in survivors of the atomic bomb detonations in Hiroshima and Nagasaki, relative to that of Japanese who were not exposed, in relation to the time since their exposure to the detonations in 1945. For leukemia, the pronounced increase in the relative risk during the 1950s suggests that the induction/latent period associated with this intensity of radiation could be as short as 5–10 years (or even shorter, since there are no data provided for 1945–50). The persistence of at least a small increase in risk of leukemia through the late 1970s is compatible with a maximum period for induction/latency associated with radiation exposure of at least 30 years.
In some circumstances, nearly all cases of disease among exposed individuals are due to the exposure (i.e., the attributable risk percent is close to 100%). For example, the association between in utero DES exposure and vaginal adenocarcinoma is so strong that almost no cases arising in a given cohort exposed to DES would be expected had DES not been used (Herbst et al., 1971). In this circumstance, the distribution of the length of the induction/latent periods after DES exposure can be assessed simply by enumerating the times when cases occur following exposure. Since the period of exposure was restricted to the nine months prior to birth, the range of incubation/latent periods following exposure can be gleaned, approximately, from the age distribution of the cases at the time of their diagnosis.
Occasionally, an examination of variation in disease occurrence across populations, or within a population over time, can offer strong clues regarding the minimum duration of the induction/latent period associated with a particular exposure.
Example 17-3. Infection with hepatitis B virus is a strong risk factor for hepatocellular carcinoma (HCC). In Taiwan, mass immunization in newborns against hepatitis B infection began in July 1984, because of the extensive transmission of the virus at that time of life. To evaluate the possible early impact of this program on the incidence of HCC, Chang et al. (1997) analyzed data from the records of the Taiwan Cancer Registry through 1994. They identified three cases of HCC among the cohort of 6–9-year-old children who had been born between 7/84–6/86, a cohort in which 85–90% of the children had been vaccinated. Based on the rates in 6–9-year-old children born during 7/74–6/84 (almost none of whom would have been vaccinated), 12 cases would have been expected among children in the later cohort (relative risk = 0.25). This dramatic reduction suggests, not only that the vaccine has been efficacious, but that the induction/latent period for liver cancer after hepatitis B infection in the perinatal period can be as short as 6–9 years.
For etiologic exposures that are prolonged (e.g., aflatoxin consumption, cigarette smoking), there is no known point in time that can be specified as being the one at which the accumulated exposure is first able to cause disease, and after which additional exposure does not continue to add to the risk. Studies of these agents in relation to disease occurrence can examine the variations in relative risk as a function of time since first exposure, cognizant that the range of time periods during which elevations are present may well not correspond to the range of induction periods following a cumulative dose of an exposure that is adequate to give rise to disease.
Influence of the Suspected Induction/Latent Period on Study Design
Short Induction/Latent Periods
In many instances, the close connection in time between an exposure and the development of a rare illness makes possible the identification of an association between them. For example, because anaphylaxis has been observed to follow so soon after the administration of parenteral penicillin therapy, a causal relationship has been inferred despite the absence of contemporaneous data on the incidence of anaphylaxis in a non-exposed group. The incidence of such dramatic and unusual symptoms in any short period of time is presumed to be vanishingly small in the absence of a recent injection of penicillin (or some other drug).
When there are numerous causal pathways that can lead to a given illness, including some that do not involve the exposure in question, we need formal epidemiologic studies that include an explicit basis of comparison to document the presence and magnitude of an association. However, the presence of a very short induction period can pose problems in this regard. For example, it is plausible on toxicological grounds that consumption of a large quantity of alcohol could predispose acutely to the occurrence of a myocardial infarction. A cohort study could not be expected to examine this issue, since it would not be feasible to identify the very large number of inebriated persons necessary to observe any appreciable number of infarctions during the few hours they remain inebriated. Similarly, a study that compared blood alcohol levels between cases and controls would be unlikely to provide a valid result: Even if it were possible to obtain a blood sample by which to estimate recent alcohol consumption on each case, the generally available means of recruiting controls—which require making appointments in advance and obtaining informed consent—would almost certainly result in a group in which the proportion of inebriated persons would be atypically low.
Nonetheless, there are circumstances in which: (a) exposure status in the population under study can be accurately ascertained; and (b) it is possible to correctly estimate the duration of the period of presumed altered risk immediately following the onset of exposure. In such a circumstance, a comparison of the incidence of the outcome in question during that period relative to the incidence at other times could provide a valid assessment of the short-term impact of the exposure.
Example 17-4. Investigators in Denmark sought to evaluate the occurrence of febrile seizures in children who received the newly introduced (in 2002) acellular pertussis vaccine (Sun et al., 2012). Using data from the Danish Civil Registry to enumerate cohort members, the Danish Health Registry to ascertain the date of receipt of this vaccine (in combination with diphtheria tetanus toxoid, inactivated poliovirus, and Haemophilus influenzae type B vaccines), and the Danish National Hospital Register, they could calculate the incidence of febrile seizures leading to hospitalization during the week following vaccination, as well as the corresponding incidence in other weeks. In this study, because there were reasons to believe that vaccination would have no lingering influence on the likelihood of a febrile seizure after one week, the large majority of Danish infants identified contributed to the person-time denominator during both the “exposed” and “non-exposed” intervals. Because the incidence of febrile seizures rises rapidly with increasing age during infancy, it was necessary to tightly control for age in this analysis.
Some comparisons of the incidence of a health outcome shortly after an exposure involve only persons who actually sustain the outcome. The approach used—termed the “self-controlled case-series” method (Whitaker et al., 2006; Weldeselassie et al., 2011)—asks whether the outcome occurred more often in a given period of time proximal to the time of the exposure (the risk interval) than would have been expected based on the proportion of the total period of follow-up represented by the risk interval.
Exposures that rapidly give rise to disease can sometimes be identified in case-control studies that obtain exposure information by means of interviews. For example, Siscovick et al. (1984) found that, of 133 Seattle-area residents ages 25–75 years who sustained a primary cardiac arrest during a 14-month period, nine were engaged in vigorous physical activity at the time (based on reports of spouses or other bystanders). This proportion—9/133—was some 50 times greater than expected based on the proportion of time a sample of demographically similar persons was reported (by spouses) typically to be engaged in vigorous physical activity. However, just as for case-control studies in general:
• The validity of studies investigating possible short-term effects rests on the comparability of exposure ascertainment between cases and controls. In the above example, there probably was some non-comparability of reporting of vigorous exercise by witnesses of a cardiac arrest on one hand, and persons reporting the usual patterns of vigorous activity of their spouses on the other. Thus, while a 50-fold case-control difference almost certainly must be attributable to more than differences in the means of exposure ascertainment, a much more modest difference could be entirely explained on that basis.
• The power of a case-control study to evaluate a short-term etiologic relationship is often low, due to the rarity of the relevant exposure. For example, if it is hypothesized that it is only the initiation of a pharmacological therapy that is associated with an increased risk (e.g., new use of a product containing phenylpropanolamine and hemorrhagic stroke (Kernan et al., 2000), or the recent cessation of such a therapy (e.g., discontinuation of beta blocker use in relation to the incidence of coronary heart disease (Psaty et al., 1990)), then only moderate or large associations can be reliably identified in even the largest case-control studies.
Close relatives of case-control studies—case-crossover studies, also are used to assess the influence of some short-term risk factors (Maclure, 1991). These studies compare a case’s exposure status at the time of the onset of his/her illness to that person’s expected exposure status, based on his/her past history, obviating the need for a separate control group. For example, among persons who had recently sustained a myocardial infarction, one could contrast their alcohol consumption during the hour or two prior to the event and that predicted based upon their usual pattern of consumption. Such a study would be feasible if exposure status, both recent and usual, could be ascertained accurately by means of an interview or questionnaire. It would not be feasible in situations where only recent status could be ascertained, such as if one were estimating alcohol intake from levels in blood drawn at the time of the infarction.
Considerations pertaining to the design, analysis, and interpretation of case-crossover studies have been discussed in detail by Redelmeier and Tibshirani (1997). Briefly, the analysis of these studies proceeds like that of a matched case-control study (see Chapter 15), in which each study subject acts as his/her own control. The interpretation of the results will be influenced by the ways in which questions such as the following are answered:
• How much misclassification of exposure status may have occurred from incorrectly judging the length of the relevant “window” of exposure prior to disease onset? For example, what if heavy alcohol consumption predisposed to myocardial infarction not just during the several hours when blood alcohol levels were above a certain threshold, but for several more hours or days (as a result of some delayed physiological response)? An analysis that labeled as “exposed” only the subjects with heavy consumption immediately before the infarction would mis-assign the exposure status of some subjects, reducing the study’s ability to detect an association.
• To what extent was the confounding influence of other exposures taken into account? By having a person serve as his/her own control, confounding by factors that do not vary to any appreciable extent over short periods of time (e.g., demographic characteristics) is reduced or eliminated. However, there remains the possibility of confounding by risk factors that do vary over time in relation to the exposure. For example, if heavy alcohol consumption were always accompanied by cigarette smoking, and the latter acutely predisposed to myocardial infarction, a spurious association between alcohol and myocardial infarction could be deduced.
Long Induction/Latent Periods
As indicated in the earlier example of aspirin consumption in relation to the incidence of colorectal cancer, many randomized trials are not designed to extend over a long enough period to be able to identify a delayed impact of an exposure. Facing the same problem are cohort studies of newly exposed persons that initiate follow-up around the time the exposure has taken place. Alternatively, if an exposure sustained in the past can be ascertained by means of interviews or records, then it is feasible for both case-control studies and cohort studies that use these sources of information to address the possible long-term impact of the exposure. However, if a study subject’s exposure status cannot be ascertained in retrospect—as would be likely to happen, for example, in a cohort or case-control study among middle-aged women that wished to investigate whether breast cancer risk is associated with levels of endogenous sex hormones during puberty—then there are no attractive options. One tries to either: (a) identify measurable correlates of the exposure that can be measured retrospectively (in this case, perhaps, a weak correlate such as age at menarche); or (b) identify a valid “surrogate” outcome, a condition that strongly predicts the later appearance of the disease of interest. (For breast cancer, no such surrogate outcome has yet been identified. For a condition such as colon cancer, however, the surrogate might be the occurrence of an adenomatous polyp.) A third alternative would be (c) to conduct a very long (and thus very expensive) cohort study with prospective follow-up.
Example 17-5. Efforts to assess the potential role of micronutrient deficiencies in the etiology of stomach cancer have been hindered, in case-control studies, by difficulties in the measurement of exposure status: Recall of past diet does not provide accurate information regarding intake of most micronutrients, and measurement of serum micronutrient levels in cases after a diagnosis of stomach cancer may not yield values indicative of those present during the genesis of the cancer. In order to overcome these problems, You et al. (2000) conducted a cohort study in Linqu County, China. At baseline in 1989–1990, serum was drawn for determination of micronutrient levels, and an endoscopy was performed in which a biopsy specimen was obtained. The latter was repeated in 1994. The presence of gastric dysplasia at baseline was a strong risk factor for the development of gastric cancer: Persons with dysplasia had some 30 times the risk as those with normal mucosa or with lesions no worse than superficial gastritis or chronic atrophic gastritis. Therefore, the investigators felt justified in considering the development of dysplasia during the follow-up period as a relevant endpoint, in addition to the development of gastric cancer per se. In the approximately 400 subjects on whom micronutrient levels had been measured at baseline and in whom gastric dysplasia had not been present at that time, gastric biopsies revealed that 60 had progressed either to dysplasia or cancer by 1994. Had the authors restricted the analysis to the incidence of cancer alone, only a handful of cases (<10) would have been present from which to draw any inferences.
As much as lengthy induction/latent periods can be a challenge and frustration to the researcher, they can be a blessing to those who are trying to prevent disease. Whatever exposures in early reproductive life are involved in the etiology of breast cancer, they do not usually give rise to the disease until two or more decades later. This delay allows time to attempt interventions (e.g., administration of a steroidal estrogen-response modifier, such as tamoxifen or raloxifene, to women judged to be at high risk) that have the potential to block the causal influence of those earlier exposures.
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1. Phenylpropanolamine (PPA) is a sympathomimetic agent that, until November 2000, was a component of a number of over-the-counter decongestant medications sold in the U.S. for treatment of cough and flu symptoms. Based on the pattern of events described in some case reports submitted to the Food and Drug Administration, it was hypothesized that in rare individuals, initiation of use of a PPA-containing medication could promptly (within one day) give rise to a hemorrhagic stroke.
Let us say that during the time PPA was being used in decongestants, the manufacturers of these drugs approached you to design a study to test the above hypothesis. Because immense resources would have been required to conduct a randomized trial or a cohort study of a rare event such as hemorrhagic stroke—rare during a given one-day period—you believe that a case-control study is the only feasible approach. And, there being no practical alternative, you decide that information regarding newly initiated PPA use would come from the survivors who were able to provide an interview. You would like to choose controls from persons demographically similar to the cases. In the population in which the study is to be done, such controls can be identified and recruited by means of random-digit dialing of telephone numbers. An in-person interview would be conducted as soon as possible among those willing to participate, and (to reduce recall bias) these persons would be asked questions about their use of PPA-containing medications in the day prior to interview.
When you propose this design to the manufacturers, they (gently) suggest that because a substantial fraction of potential controls asked to participate in fact do not do so, and because others delay the interview for reasons of illness, a spuriously high odds ratio associated with recent initiation of a PPA-containing medication might be obtained. Why is their concern likely to be a valid one?
2. In their article “Carcinogenicity of lipid lowering drugs,” Newman and Hulley (1996) contend that “all members of the two most popular classes of lipid-lowering drugs (the fibrates and the statins) cause cancer in rodents, in some cases at levels of animal exposure close to those prescribed to humans. [However,] evidence of carcinogenicity of lipid-lowering drugs from clinical trials in humans is inconclusive.”
The results of clinical trials published by mid-1996 indicated that the incidence of cancer (overall) was nearly identical after five years of follow-up in users of simvastatin and placebo (Scandinavian Simvastatin Survival Study Group, 1994) and in users of pravastatin and placebo (Shepherd et al., 1995), respectively. By “inconclusive,” Newman and Hulley no doubt were referring to the relatively small number of cancer cases identified in these studies (collectively, only about 200 in users of a statin), and especially to the much smaller number of cancers of individual sites. What do you believe was another important reason for their reluctance to accept the results of these well-done trials as assurance of no increased risk of cancer associated with long-term statin prophylaxis?
3. To test the hypothesis that wearing a helmet while skiing could reduce the risk of head injury, Hagel et al. (2005) compared the proportion of helmet users between skiers who sustained a head injury and those treated for injuries of other parts of the body. Concerned with potential confounding by characteristics of skiers that might be related both to helmet use and to the risk of head trauma, the study also compared the proportion using a helmet on the day of their head injury and on the day of their previous skiing outing. Potentially offsetting the benefit of this latter, case-crossover, approach, is: (a) the possible incomparability of ascertainment of helmet use between the two days; and (b) characteristics of the two days (e.g., visibility) that could be related to the decision to wear a helmet and also to the risk of sustaining a fall. What is a possibly even larger obstacle to the case-crossover approach’s being successful in identifying a true association between helmet use while skiing and a reduced risk of head injury?
1. The purpose of the control group in this study is to estimate the proportion of the underlying population at risk who began to use a PPA-containing medication during any given recent one-day period. Persons with symptoms towards which these medications are directed (colds, flu) might be more inclined to decline to participate than other persons and, if they agreed to participate, might choose to postpone the interview until they expected to recover. For these reasons, the proportion of the interviewed controls reporting very recent initiation of medications containing PPA would probably be smaller than the proportion in the population from which they had been sampled. Since this same source of bias cannot exist for the cases—they are recalling a one-day period prior to a fixed point in time; i.e., the time the first symptoms of their stroke occurred—a falsely high odds ratio will ensue.
To reduce bias from this source, the information from the controls can refer to an earlier one-day period. For example, when studying this question, Kernan et al. (2000) chose a period ending up to one week prior to the time of interview. Even though the latter choice runs the risk of a greater degree of incomplete recall by controls than would asking about the day immediately prior to the interview, overall it would seem to produce a more valid estimate of the frequency of new use of PPA in the population.
2. It may require more than five years of statin use to produce an increase in the risk of one or more forms of cancer. Alternatively, it may require a period of time after even five years of use for cancers caused by such use to manifest themselves. Studies that have not followed statin users for more than five years cannot address these possibilities.
3. For only 35 of the 1028 skiers who sustained a head injury did helmet use differ between the day of the injury and the previous day on which they skied. Thus, there was not a great deal of statistical precision in the case-crossover analysis. The odds ratios associated with wearing a helmet that were obtained in the case-crossover and case-control portions of the study were quite similar—0.6 versus 0.7, respectively—but the confidence interval for the case-crossover odds ratio was considerably wider: 0.3–1.2 versus 0.6–0.9.
Case-crossover studies could provide information regarding exposures that have a short-term influence on risk of disease or injury, but that potential cannot be realized if there is little intrapersonal variation in exposure status over time.