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A recent article (1) in Obesity addressed methodological issues in studies of BMI and mortality. Greenberg (1) explored some aspects of the association between BMI and mortality as found in the National Health and Nutrition Examination Survey (NHANES) I data to evaluate the effects of regression dilution and of reverse causation and raised several important issues that merit discussion. His stated goal was to extrapolate his findings to those of the 2005 study of Flegal et al., which analyzed excess deaths as related to BMI category (2), and which used data from NHANES I as well as from NHANES II and III. We offer some comments on Greenberg's approach and discuss some of the issues raised regarding our NHANES analyses. NHANES I data were originally collected in 1971–1975 from a nationally representative sample of the US population. As part of the NHANES I Epidemiologic Follow-up Study (NHEFS), body weights of survivors were re-measured in 1982–1984. Flegal et al. (2) used the 1971–1975 NHANES I data set as the baseline, used the sample weights in their analysis, used age as the time line and allowed for effect modification by age. In addition, building on the approach developed by Allison et al., (3) Flegal et al. (2) combined the relative risk estimates obtained from NHANES data with other nationally representative data sources to arrive at population estimates of excess deaths. Greenberg (1) used different data and procedures. In particular, he used the 1982–1984 NHEFS as his baseline data, apparently analyzed the data without sample weights, used calendar time rather than age, did not allow for effect modification by age and derived attributable fraction and excess deaths estimates for the unweighted NHEFS sample rather than for the US population. In addition, unlike Flegal et al., (2) Greenberg apparently did not take the NHANES I complex sample design into account when computing the standard errors for his estimates. As a consequence Greenberg's confidence intervals may well be too narrow (4). Regression dilution refers to bias toward zero (i.e., “attenuation”) of estimates of a regression coefficient that results from measurement error and within-individual variability in the exposure variable (5). The measurement error for weight in NHANES is small, however. The Pearson correlation of 0.88 between the NHANES measured weights of 1971–1975 and 1982–1984 indicates that these weights are quite stable. To reduce the effects of regression dilution, Greenberg averaged the weight data for the periods 1971–1975 and 1982–1984. The correlation of the 1982–1984 weights with the average weights is 0.97. Thus, in using the average weight rather than the weight data of 1982–1984, Greenberg found only small effects on relative risks (as shown in his Figure 2b), a result similar to that found by Clarke et al. (5). Even though there is little numerical change from using the average weight, rather than the baseline weight as used by Allison et al. (3) and others, one should bear in mind that the use of the average weight is meant to address a different issue than does the use of the baseline weight and should therefore not be considered a correction. The use of average weight would address the effects of “usual” weight over a long time period rather than of weight at the beginning of a specified year. Allison et al. (3) clearly indicated that their goal was to estimate the effects for a given year based on the weight at the beginning of that same year. Figure 1a in Greenberg (1) is a potentially misleading portrayal of the variability in serial weight measurements because it reflects the selection phenomenon of regression to the mean, in addition to the actual variability of the weight data. Regression to the mean is a statistical phenomenon that makes the natural variation in repeated data look like a real change (6,7). Whenever individuals are grouped by the value of a measurement at one time point, then among those with extreme values on that measurement, the values of the measurement at a second time tend to be less extreme, even in the absence of systematic secular trends. Greenberg's Figure 1a shows this expected phenomenon for the repeated measurements in NHANES because individuals are grouped into categories based on the 1982–1984 BMI. Thus it appears that people who ended up with a low BMI in 1982–1984 lost considerable weight and those who ended up with a high BMI gained considerable weight; these apparent large weight changes are mainly the result of the grouping by the 1982–1984 BMI and regression to the mean. Greenberg (1) examined the effects of changing the BMI reference category. As the reference category became narrower and closer to the nadir of the BMI–mortality curve, he found that estimates of obesity-associated excess deaths increased, as was also found by Flegal et al. (2) We found that with a change in reference category from BMI 18.5–<25 to BMI 23–<25 our estimate of obesity-associated excess deaths based on the relative risk estimates of NHANES I increased by 11%. Greenberg, however, by making the same change in the reference category found a percentage increase in obesity-associated excess deaths of 115%, i.e., more than ten times higher. This example alone shows that Greenberg's estimates cannot accurately be extrapolated to the results of Flegal et al. (2), presumably because of the numerous differences in the data and methods used by Greenberg. Reverse causation refers to a situation in which the outcome affects the exposure, rather than the reverse. However, in the context of obesity epidemiology, the term “reverse causation” has come to refer to a hypothesized effect on the BMI–mortality relationship of illness-induced weight loss before baseline in individuals who subsequently die of the same illness (8). This phenomenon might more properly be regarded as confounding, or as effect modification due to illness, rather than as true reverse causation, because the outcome (mortality) does not affect the exposure (body weight). Willett et al. (8) point out that people frequently lose weight as a consequence of an illness that is ultimately fatal. For such weight loss to affect BMI–mortality analyses, it must occur prior to baseline. Indirect methods are generally used to exclude participants who might have illness-induced weight loss before baseline and subsequent mortality due to the same illness, such as excluding all participants with a history of illness or all participants who have lost weight or all participants who die in the first few years of the study, without specifically identifying participants who had illness-induced weight loss prior to baseline. Estimates from the Atherosclerosis Risk in Communities Study based on measured weights 3 years before baseline, early deaths and pre-existing illness (9) suggested that only ∼0.3% of the baseline population in that sample consisted of people who died within 4 years after baseline and had sufficient weight loss prior to baseline so as to change their BMI category from >30 to <30 or from >25 to <25. That study also did not unambiguously identify participants with illness-induced weight loss and subsequent mortality. Exclusions to address the effects of illness-induced weight loss (not to be confused with exclusion of participants based on smoking history, which addresses a different issue than reverse causation (8)) have shown mixed effects on relative risk estimates. In the Physicians' Health Study (10) relative risk estimates increased by 0.02–0.23 after excluding early deaths and people with unstable weights, who might have had illness-induced weight loss. In the Nurses Health Study (11), similar exclusions caused relative risk estimates to increase by 0.1–0.4. In the Health Professionals Follow-up Study (12), however, relative risk estimates decreased by 0.01–0.04 in overweight and obese weight categories after such exclusions, suggesting little or no impact from reverse causation bias. Several other large, carefully conducted epidemiologic studies with measured weights and heights have found little or no impact of such exclusions on the association between BMI and mortality (13,14). Greenberg (1), as well as Lawlor et al. (15) and Manson et al. (16), invoke reverse causation to try to explain the finding by Flegal et al. (2) that all-cause excess deaths associated with obesity were higher when NHANES I relative risks were used than when relative risks from NHANES II and III were used. Greenberg (1), Lawlor et al. (15), and Manson et al. (16) suggest that there is less reverse causation in NHANES I because the follow-up time for NHANES I was longer than that in the other surveys. However, this suggestion is not supported by the data. As noted in our original article (2), even after only 10 years of follow-up, estimates of obesity-associated excess mortality based on NHANES I relative risks were higher than those based on the later surveys. In fact, estimates of obesity-associated excess deaths based only on NHANES I relative risks are 275,248 using 10 years of follow-up, 288,198 using 20 years of follow-up, or 298,938 using the almost 30 years of follow-up now available. Furthermore, at any given length of follow-up, estimates for obesity-associated excess mortality based on NHANES I relative risks are always higher than estimates based on NHANES II relative risks. Thus differences in length of follow-up do not explain differences in obesity-associated excess deaths across the surveys. Either reverse causation has little effect on these estimates, or reverse causation does not vary by length of follow-up. In analyses that used simultaneous exclusions based on smoking history, pre-existing illness, weight loss, early deaths, and age at measurement (2,17,18), we found no evidence that reverse causation (illness-induced weight loss prior to baseline) was an important factor in any of these surveys or that it varied across surveys. Greenberg additionally speculated that the higher upper age limit in NHANES III led to additional reverse causation and thus lower estimates. We had explored using an upper age limit of 74 years in NHANES III, to correspond to NHANES I and II, but found that such a limit had only slight and unsystematic effects on our results. As we noted previously (2), the differences between NHANES I and the later surveys suggest the possibility that the association of obesity with total mortality may have decreased over time, perhaps due to improvements in public health or medical care for obesity-related conditions. This would also be consistent with the well-known decreases in cardiovascular disease mortality (the main cause of excess mortality among the obese) over time and the increases in life expectancy at the same time when the prevalence of obesity was increasing. However, as we noted (2), such differences could have also been due to chance variation. Greenberg stratified the NHEFS sample by using the presence or absence of serious illness at baseline and found seemingly different relative risks between the two strata. Although he did not present evidence that the differences were statistically significant or that the differences were specifically due to illness-induced weight loss, he attributed them to reverse causation. Greenberg then used attributable fraction methodology to estimate the effects of regression dilution and reverse causation. He calculated the obesity-attributable fraction of deaths in NHEFS with a computational formula (his equation 1) that combines the prevalence of obesity among decedents (P), with the hazard ratio for obesity (HR). This computational formula is valid when applied correctly to internally consistent data from a single cohort (19,20), but Greenberg applied it to data that were not internally consistent. For the formula to be applied correctly, P and HR should both be calculated from the same data, and P should be based on a consistent definition of obesity that identifies the same individuals as obese as those who were identified as obese for the calculation of HR (10). For some analyses, however, Greenberg appears to have inappropriately defined P for obesity using 1982–1984 weight data but defined HR for obesity using the average of the 1971–1975 and 1982–1984 weight data. A more serious error is that Greenberg “corrected” estimates for reverse causation by using his formula 1 with an estimate of HR from the well stratum only, but with an estimate of P from decedents in the entire sample, so that P and HR were not calculated from the same data. This is not an estimate corrected for reverse causation for the NHEFS sample, because if the HR were different in the NHEFS sample, then P, the prevalence of obesity among decedents, would also have to be different. P and HR are algebraically related, and, as long as other factors remain constant, HR cannot change without P also changing. Greenberg compared and interpreted various quantities derived by these methods. As we have indicated, his procedures do not estimate the quantities of interest, cannot be recommended to estimate “corrected” attributable deaths, and have little bearing on the estimates by Flegal et al. (2) The problems in the calculation and interpretation of attributable fractions reiterate the need for caution in using attributable fraction methodology (19,20). Analysis and interpretation of associations between mortality and an individual time-varying characteristic, such as BMI, that may be modified by changing health status, are difficult. Prospective serial data on health status and BMI would be ideal for such analyses, but are seldom available. In addition to data limitations, one must be aware of the strengths and limitations of available analytic approaches, many of which have been touched on in this commentary. The authors declared no conflict of interest. The findings and conclusions in this report are those of the authors and not necessarily of the agency.
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Flegal et al. (2008) studied this question.
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