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Diet and health risk: risk patterns and disease-specific associations ^{1 ,2}

	ABSTRACT

TOP ABSTRACT INTRODUCTION HOW LARGE A RELATIVE... DOSE RESPONSE THRESHOLD EFFECTS DISEASE-SPECIFIC RELATIVE RISKS CONCLUSIONS REFERENCES

 
Whether such epidemiologic descriptors as relative risk, dose response, and threshold points convey meaningful information is often the subject of debate. Thus, using these descriptors to juxtapose the many disease-specific effects of nutritional exposures becomes problematic. In this article it is argued that epidemiologic patterns of disease-exposure associations must be interpreted in light of the profound imprecision of exposure assessment that characterizes nutritional epidemiology. In general, this imprecision leads to substantial attenuation of disease-exposure associations, such that relative risk, dose response, and the extent to which there are thresholds in disease-exposure associations can be seriously underestimated. Linking disease-specific relative risks, especially when derived from different studies with different methods of assessing exposure, is made increasingly difficult. The most critical tasks for lessening bias in these epidemiologic descriptors are first, to lessen imprecision in measuring exposures, and second, to adjust association estimates for attenuation due to measurement imprecision.

Key Words: Epidemiology • relative risk • attributable risk • measurement error • reliability • validity • disease • exposure

	INTRODUCTION

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In the past several years we have seen numerous statements about the translation of epidemiologic research findings into generalizations about health risks, with the association of this or that exposure with the risk of this or that disease taken to imply that the exposure is either healthful or hazardous. Whether the associations truly signal that the hazard or benefit linked with the exposure is meaningful as opposed to trivial is the subject of a great deal of debate.

The purpose of this article is to consider 3 problems of relating epidemiologic findings to health outcomes. The first is the size of the relative risks associated with exposures and how large those relative risks need to be, in general, to be useful or informative. The second is the presence of a dose response or, conversely, the presence of thresholds in the data. The third problem is in the evaluation of disease-specific relative risks.

Precise quantitative descriptions of the association of nutritional exposure with disease risks are needed. We need to know what professionals should emphasize. Those who will use our advice want to know how much they can decrease their risk by avoiding a food item. Would they profit more from increasing their intake of one food by some percentage or from decreasing their intake of another food by that same percentage ( 1 )? Is the effect of an exposure noteworthy for those with a given risk profile? Might several foods interact in increasing or decreasing their risk ( 2 )? Does the consumption of a food decrease the risk of one disease enough that people should increase their consumption of it?

Obtaining this information requires precise measurement of the effects of exposure on risk. This in turn requires precise measurement of either exposure or of the extent and structure of measurement error in the exposure data. Knowing that there is greater correspondence between measured and true exposure than would be expected on the basis of random chance with no correspondence between observed and actual exposure is not enough ( 3 ).

	HOW LARGE A RELATIVE RISK IS MEANINGFUL?

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To individuals, vulnerability to disease is critical. That is what individuals are interested in understanding. The relative risk, widely used as a means of summarizing the effect of an exposure on risk, is the risk among those exposed to a supposed agent divided by the risk among those not exposed to it. A relative risk >1 implies that risk is higher among the exposed and a relative risk <1 implies that risk is lower among the exposed. It is common for relative risks to be described in causal language; thus, it may be stated that an exposure with a relative risk >1 increases risk and that one with relative risk <1 decreases risk. Such causal assertions are often not well justified by the data. In the many situations in which experiments have not been performed, these assertions are particularly risky. It was common for several years, for example, to interpret the epidemiologic observation that ß-carotene in the diet or blood was associated with decreased risk of several epithelial cancers to mean that ß-carotene in the diet decreased risk ( 4 , 5 ). Experimental studies have cast doubt on this causal interpretation ( 6 – 8 ).

An individual's vulnerability depends not only on the size of the relative risk associated with exposure but also on the baseline risk of disease. The actual risk among exposed individuals in a population is determined by baseline risk—that is, the risk among the nonexposed—multiplied by the relative risk imposed by exposure. If, for example, the relative risk was 20, and the probability of disease among the nonexposed was 1/1000, then the probability of disease among the exposed would be 2%. Clearly, a sufficiently large relative risk can subject the exposed to substantial risk even with low baseline risk. With a probability of disease among the unexposed of 1/1000 and a relative risk of 100, the probability of disease among the exposed is 10%. However, it is necessary for such relative risks to be large. The only instance in which a relative risk approximating 100 has been seen was from joint exposure to aflatoxin and hepatitis B as a risk factor for liver cancer ( 9 ).

Debates in epidemiology are less about huge relative risks than about small ones, over the interpretation of relative risks such as those of 1.3 to 2 or even 2.5 ( 10 ). If exposure to a nutritional agent is widespread, a relative risk of even 1.2 can mean that a substantial proportion of disease is related to the exposure. However, such relative risks do not alter risk a great deal. In addition, such relative risks can readily result from study errors, including response bias, report bias, and confounding. One study shows that a strong confounder measured poorly can distort a relative risk of 1 associated with an exposure, making it appear to be as large as 1.5–2 or even larger, and that this distortion can persist with standard statistical control for the confounder ( 3 ).

Two other descriptors of risk—the attributable risk and the etiologic fraction—are used as means of applying epidemiologic data to health policy questions. The attributable risk is the risk in a population associated with a given exposure and is calculated as the numerical difference between risks in the exposed and the unexposed. This attributable risk—the risk among the exposed minus that among the nonexposed—is usually similar to the risk among the exposed because the risk among the nonexposed is negligible.

The etiologic fraction is the percentage attributable risk or the attributable fraction ( 8 ). This reflects the proportion of the total burden of disease that is associated with a given exposure; conversely, it describes the proportion of disease that could be eliminated if the exposure were eliminated. It is dependent on the prevalence of exposure and the relative risk imposed by exposure. The etiologic fraction according to the relative risk associated with exposure and according to the percentage of the population exposed is shown in Table 1 . What is most striking is that a nutritional factor that imposes even slight relative risks can be responsible for a sizable percentage of disease risk within a population exposed to the risk factor. For example, an exposure that, with prevalence of 50%, multiplies risk by 1.5 times can be responsible for 20% of the disease in a population.

The attributable risk and etiologic fraction are defined by the relative risk; bias and imprecision associated with the relative risk result in bias and imprecision in the attributable risk and etiologic fraction. Small observed relative risks are especially likely to have issued from bias ( 1 , 10 ); this should underscore the degree to which attributable risk and etiologic fractions drawn from those relative risks must be interpreted with caution.

However, observed relative risks issuing from large true relative risks can be greatly attenuated by even modest measurement error. The relative risks that would be observed given the true relative risks, according to the degree of misclassification or measurement error, are shown in Table 2 . With exposure misclassification of only 5%, true relative risks of 5, 50, and 100 would appear to be 4, 27, and 43, respectively. If, as may be common in nutritional epidemiology, exposure misclassification probabilities are in the vicinity of 30%, the observed relative risks associated with true relative risks of 5, 50, and 100 are 1.8, 3.5, and 3.9, respectively. Note the convergence of large and modest relative risks with increased measurement error. Thus, measurement error limits the investigator's ability to distinguish substantial from modest relative risks. Exposure misclassification of 30% is likely in nutritional epidemiology research. Thus, the relatively modest relative risks observed could quite possibly result from huge relative risks obscured by measurement error.

	DOSE RESPONSE

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Dose response is used to indicate the degree to which risk increases monotonically with increasing exposure. Dose response was viewed by Hill ( 11 , 12 ) as one of the signal indicators of a cause-effect relation between exposure and disease. Hill suggested that, with risk increasing steadily with increasing exposure, the relation between exposure and risk could be more readily interpreted as causal. Rothman and Greenland ( 12 ) criticized this logic, pointing out that it is readily possible for a spurious association of exposure and disease to appear as dose response.

Exposure to many environmental hazards, including nutritional ones, can be graded. It is intuitively reasonable to expect that, in general, the degree of risk imparted would increase with increasing exposure to a true pathogen. Alternatively, it might be possible to grade the probability that an individual has been exposed to a pathogen; the probability of disease could increase with increasing certainty that exposure to a true pathogen had occurred. However, the existence of a dose response must be interpreted carefully. An investigator evaluating a pattern produced by different amounts of error in a case-control study can, by creative collapsing of exposure categories, extrude a dose-response pattern even in the absence of any true association of exposure and risk ( 13 ). The correlates of a variable that modifies risk in a dose-response fashion could be similarly linked to risk.

The absence of a dose response might seem to cast severe doubt on the likelihood that a true causal association has been identified. However, the substantial measurement error typical of nutritional epidemiologic studies can exert an overwhelming effect, lessening the extent to which a true dose-response pattern in the data would be apparent. Freudenheim and Marshall ( 14 ) showed that profound measurement error can severely mask evidence of a dose response. The effects of strong and moderate dose-response patterns obscured by exposure measurement containing profound or severe errors are shown in Table 3 . These data are drawn from samples of simulated case-control studies, each with 300 cases and 300 controls. Two patterns are evaluated: in the first, with strong risk enhancement, relative risk rises monotonically to >7 in the top exposure quintile; in the second, with moderate risk enhancement, relative risk rises monotonically to 2.4 in the top exposure quintile. On average, observed risk tends to monotonically increase with increasing exposure even in the presence of profound measurement error. Although a dose response in the data would tend to persist, exceptions for individual studies would be common ( Table 4 ). Thus, for the pattern of strong risk enhancement displayed in Table 3, with studies of 300 cases and 300 controls, the test for trend was always statistically significant; it was nearly always significant for the pattern of moderate risk enhancement. With profound error, though, there was a >10% probability that the test for trend would not be significant even for the pattern of strong risk enhancement. With a pattern of only moderate risk enhancement, the probability of a nonsignificant trend test was 66%.

An important indicator of dose response is the extent to which the odds ratio associated with the highest exposure category is higher than the odds ratios associated with the second, third, and fourth exposure categories. Table 4 shows that, with a strong pattern of risk enhancement, the fifth category odds ratio is always greater than that for the second and third categories and is nearly always greater than that of the fourth category. Profound measurement error substantially increases the probability that at least one of the intermediate category odds ratios is greater than that of the highest exposure category. Profound measurement error has a similar effect if the exposure has a more moderate effect. The probability of the second or third quintile odds ratio exceeding that of the fifth quintile is slight with actual exposure measured, but profound measurement error increases that probability to between 20% and 25%. Even in the absence of measurement error, there is a nearly 1 in 5 chance that the fourth category odds ratio would exceed that of the fifth; profound measurement error increases that probability to nearly 38%.

A reasonable conclusion is that with relatively accurate measurement of exposure to a suspected etiologic nutritional agent the absence of a pattern of dose response offers compelling evidence either that the exposure is not causally related to risk or that the effect of exposure on risk is nonmonotonic. The presence of substantial measurement error, though, greatly limits the investigator's ability to draw either conclusion.

A related question concerns how a test for trend is juxtaposed to the size of relative risk in a comparison of extreme exposure categories, comparing, for example, the first and fifth categories of exposure. Does a significant test for trend mean that a modest or even trivial relative risk is noteworthy or of public health significance? Most trend tests—the Mantel-Haenszel extension test is the best example—are not descriptive but inferential. They are influenced not just by the strength of the association but also by the size of the sample; alone, their statistical significance indicates nothing about the strength of the association of nutritional exposure and disease risk. A weak trend in a large sample may be statistically significant, even if the relative risk imposed by exposure is trivial, whereas with a much more alarming elevation of relative risk in a smaller study, the trend test could be statistically insignificant. Walker and Blettner ( 15 ) pointed out that in the presence of measurement error the investigator must expand sample size to accommodate the attenuation of the strength of the association of exposure and risk. However, increasing sample size only increases the probability of a statistically significant trend test; it does not lessen the attenuation of relative risk resulting from measurement error.

Hunter et al ( 16 ), in a pooled analysis evaluating the effect of dietary lipid intake on the risk of breast cancer, found a significant trend test for cholesterol intake. Because the combined sample was extremely large and the relative risk elevation accompanying greater fat intake was extremely modest, Hunter et al dismissed this as indicative of no noteworthy association.

	THRESHOLD EFFECTS

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It is commonly expected within epidemiology that exposure to a true risk factor should be linked to disease risk in a pattern that resembles a dose response ( 11 – 15 ). Indeed, as noted, the existence of a dose response is often taken as evidence that a nutrition-disease risk association is real and not an artifact.

Such dose-response patterns might only be seen within a limited range of exposure: they might not be seen over the entire exposure range. There could be an exposure-risk association on one side of a fixed point; on the other side of the threshold, there could be none. An association of nutrition and disease risk might only be apparent above a given exposure level. However, it could be that exposure increases risk only up to a certain point and that beyond that point additional exposure has no effect.

Epidemiologic investigators have occasionally addressed the possibility of threshold effects. Some, for example, have suggested that there is an association between dietary fat and breast cancer risk but only below a range of 15–20% of energy from fat: beyond that range everyone is at elevated risk and additional exposure has no effect ( 17 ). This has been advanced to explain the lack of evidence that dietary fat is associated with increased risk of breast cancer in Western industrialized countries. One empirical study appears to indicate that the explanation is incorrect ( 16 ). Clearly, it is mathematically and biologically possible that risk would increase with increasing exposure only up to a point; beyond that point increasing exposure would be associated with no additional risk or even decreased risk. Risk could decline with increasing exposure only up to a point; beyond that point increasing exposure would be associated with constant or decreased risk. Although these and other patterns are without doubt possible, they have been seen in relatively few nutritional epidemiologic studies.

The existence of threshold effects raises an important issue for nutritional epidemiology. The lack of a dose response below a fixed point indicates that variation in exposure would have no effects beneath that minimal dose. The existence of a dose response only up to a fixed point suggests that alterations of exposure would have no effects beyond that given exposure. Thus, in the former situation, there would be value in lessening or limiting exposure only above the threshold. In the latter situation, there would be no value in altering exposure unless it could be reduced to less than the threshold point. The question policy analysts must ask is whether it is feasible to shift more than a trivial proportion of the population's exposure levels past the threshold point to where exposure makes a difference.

As noted, few dramatic thresholds have been observed commonly in nutritional epidemiology. However, these patterns are almost always obscured by substantial measurement error. In the presence of such measurement error, any threshold pattern can be substantially distorted. What happens to one threshold pattern in the presence of measurement error is shown in Figure 1 . It can be seen that increasing measurement error decidedly lessens the degree to which a sharp threshold point is apparent. The absence of an observable threshold pattern may not indicate the absence of a true threshold pattern associating exposure and risk: error could obscure a threshold.

View larger version (15K): [in this window] [in a new window]   FIGURE 1. Threshold effects and relative risk by measurement error.

	DISEASE-SPECIFIC RELATIVE RISKS

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It is important to consider the effect of any one exposure on the risk of any one disease in light of the entire spectrum of health threats that people face. The news that dairy products might increase the risk of ovarian cancer or that ß-carotene might increase the risk of prostate cancer might be received as causes for alarm, but the probabilities that a woman develops ovarian cancer or that a man develops clinical prostate cancer are small. What do dairy products do to the risk of heart disease and diabetes? What does ß-carotene do to risks of lung and esophageal cancer, heart disease, and macular degeneration? What about the larger picture? The number of distinct potential impediments to our continued health and survival at any one point is large. Do we not at some point need to consider the effect of any one nutrient exposure on the entire range of possible disease outcomes?

As we have shown, the effect of exposure to a nutritional risk factor depends on both the baseline risk of disease and the effect of exposure on risk. Thus, if the probability of disease is only 1 in 10000, an extremely large relative risk, such as 100, increases the probability of disease in the exposed only to 1%. With a more modest relative risk, even of 10–50, this disease remains extremely uncommon even among the exposed. However, if the disease is more common—if, for example, the probability of disease in the unexposed is around 1%—a relative risk of only 10 increases the probability of disease to 10%. It is important that even a large relative risk be evaluated in terms of the probability of disease resulting from the exposure. If the risk of disease in the unexposed is low enough, the probability of disease in even the exposed may not be appreciable.

Because the number of diseases is large, the evaluation of any exposure must be considered in terms of that total number. An exposure that alters the risk of several diseases might need to be considered more carefully than an exposure that affects only one disease. Consider a simple case: exposure x as it relates to diseases d1 and d2 . The exposure can increase, decrease, or have no effect on the risk of d 1, and it can increase, decrease, or have no effect on the risk of d2 . If the exposure increases the risk of both, increases the risk of one and has no effect on the risk of the other, or decreases the risk of one or both diseases, deciding on the desirability of the exposure is relatively straightforward. If, however, the exposure increases the risk of one disease but decreases the risk of the other, evaluation of that exposure becomes more complicated. The natures and courses of the 2 diseases, the ages at which they are likely to strike, the baseline risks in the unexposed, and the effects of the exposure on their risks must all be considered.

Fortunately, there are presently few empirical examples in which one exposure increases the risk of one disease and lowers that of another. Saturated fat intake, for example, is blamed for several cancers as well as for a substantial proportion of cardiovascular disease. There is little published empirical evidence that a diet high in saturated fat protects against anything. Carotenoids have been believed to protect against several cancers and other diseases in which environmentally induced oxidants appear to be pathogens, although recent experimental evidence has not supported these beliefs ( 7 , 8 ). An important rationale of the postmenopausal estrogen trial in the Women's Health Initiative is the need to evaluate the overall effect of estrogen in light of the fact that it increases endometrial cancer and possibly breast cancer risk but decreases cardiovascular disease and osteoporosis risk ( 18 ).

An exemplary attack on one such confusing situation, presented by Fuchs et al ( 19 ), evaluated the effect of alcohol intake on the risk of coronary heart disease and breast cancer. Evaluating the health experience of members of the Nurses Health Study, Fuchs et al observed that alcohol may decrease the risk of coronary heart disease but that it might have untoward effects on other health risks. They weighed the implications of this evidence by evaluating the effects of alcohol intake on mortality, using mortality as the common denominator of serious illness experience. They found that, in general, moderate alcohol intake is associated with lower mortality risk but that the numbers of breast cancer and liver disease deaths induced by heavier alcohol intake exceed the number of coronary heart disease deaths apparently prevented by it. The only population subset in which heavy alcohol use has any beneficial survival effect is that of nurses with preexisting heart disease.

Epidemiologists, as scientists, are most interested in the effects of exposures on the risks of single diseases. However, evaluating the overall effect of a nutritional exposure requires quantitation of the risks of the several diseases affected by that exposure. Although it might be possible to gather such information by the use of case-control and prospective studies focused on single disease endpoints, the most sensible approach would be to focus on survival. Quantitation of the effect of nutrient exposure on total, disease-free, or disability-adjusted survival appears to provide information that is critically needed. It remains true that measurement error will substantially distort any derivative quantification. To cope with these patterns, we have only 2 options. The first is to improve the accuracy of our assessments; our standard or goal must be perfect measurement, not measurement that merely improves on random chance. Only perfect measurement can be expected to eliminate measurement-error-induced attenuation of associations in our data ( 3 , 10 ). The second option is to estimate the structure of measurement error in our data sets and adjust our results to deattenuate them ( 20 , 21 ). This option requires extremely precise estimates of measurement error ( 21 ). Nonetheless, research on means of adjusting for the presence of measurement error appears to hold promise, as we seek to better translate our findings into meaningful assertions regarding the hazards and benefits linked by epidemiology to environmental exposure ( 20 , 21 ).

	CONCLUSIONS

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We directed this effort toward the use of epidemiologic data in evaluating the health risks associated with nutritional practices. First, we considered the use of relative risk and its derivatives: the attributable risk and the etiologic fraction. We also considered the presence of dose response and its meaning in nutritional epidemiologic data. We considered the absence of dose response: the threshold effect and what it suggests. Finally, we noted that any association between exposure and risk must be considered within the context of the entire range of diseases to which the individual is vulnerable.

It cannot be emphasized too strongly that our findings must be seen as through a very foggy lens, as a faint image of what must be there. Sampling bias persists as a potential problem that is always possible and always difficult to evaluate. Our inability to accurately measure the exposures with which we deal means that our estimates of the efforts of exposure are, at best, underestimates, and our ability to adjust for important confounders is severely limited. Confounding is not an exceptional, occasional problem, but is ubiquitous to the epidemiology of diet and disease. Epidemiologic inquiries are almost always designed to be as small as acceptable, the result being that sampling variability is almost always larger than is desirable. None of our methodologic efforts are adequate to counter the imposition of publication bias: the failure of researchers to submit and of editors to publish findings that do not fit well with the their own understanding. Thus, the information we extract from our assays of associations between exposure and disease—attributable risk, etiologic fraction, dose response, and threshold effects—is always estimated with serious imprecision or bias. We must face and better address this imprecision in our quantitation of exposure-disease associations as we seek to identify more healthful dietary patterns.

	FOOTNOTES

² Address reprint requests to JR Marshall, Arizona Cancer Center, College of Medicine, University of Arizona, 1515 North Campbell Avenue, Tucson, AZ 85724. E-mail: jrmarshall{at}azcc.arizona.edu.

	REFERENCES

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This Article Abstract Full Text (PDF) Purchase Article View Shopping Cart Alert me when this article is cited Alert me if a correction is posted Citation Map Services Similar articles in this journal Similar articles in PubMed Alert me to new issues of the journal Download to citation manager Citing Articles Citing Articles via HighWire Citing Articles via Google Scholar Google Scholar Articles by Marshall, J. R Articles by Chen, Z. Search for Related Content PubMed PubMed Citation Articles by Marshall, J. R Articles by Chen, Z. Agricola Articles by Marshall, J. R Articles by Chen, Z.