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COMMENTARY |
Rush Institute for Healthy Aging, Departments of Internal Medicine and Preventive Medicine, Rush University Medical Center, Chicago, Illinois.
Address correspondence to Dr. Carlos F. Mendes de Leon, Rush Institute for Healthy Aging, Rush University Medical Center, 1645 West Jackson Boulevard, Suite 675, Chicago, IL 60612. E-Mail: cmendes{at}rush.edu
UNDERSTANDING aging is, of course, the quintessence of all gerontological research. Numerous theories have been developed over the course of time, and indeed throughout history, to help researchers gain a better appreciation for the aging-related processes that lead to changes in health, well-being, social function, and other topics of central concern to older adults. The development of more sophisticated quantitative methods, such as mixed-effects regression models and generalized estimating equations, has accelerated scientists' ability to chart aging-related changes with increasing precision. This is clearly demonstrated in an excellent article by Shaw, Krause, Liang, and Bennett (2007)
, who used a mixed-effects regression model (hierarchical linear modeling in their parlance) to analyze aging-related changes in social relations. The article has a number of important strengths, including the use of nationally representative data, the breadth and depth of social outcome data, and the use of an analytic approach that quantifies changes over time with greater accuracy than more conventional techniques. In this commentary, I use the analytic approach employed by Shaw and colleagues as an example to raise a couple of thorny methodological issues that affect the analysis of aging and the analysis of change.
ANALYSIS OF AGING-RELATED CHANGE
Cohort and Healthy Participation Effects
The first issue pertains to the proper analysis of the "age" or "aging" effect itself. The analysis of aging-related effects depends on a consideration of three potential determinants of observed changes over time, which are typically referred to as age, period, and (birth) cohort effects. It is normally not possible to uniquely differentiate between these three types of effects in the setting of regression analysis, as each one effect is completely determined by a linear combination of the other two effects (Holford, 1991). Shaw and colleagues (2007) correctly pointed out that aging-related change is typically the primary issue of substantive or theoretical concern in gerontological research, which is why they organized and analyzed their data as a function of age (i.e., age at the time of each interview). They acknowledged the possibility of cohort effects, for which they adjusted in their analysis, as birth cohorts may have varied in terms of aging-related change in social outcomes once they reached older age. A period effect would have been less likely in their data, as this would have presumed noticeable secular changes in social outcomes during the 10-year duration of the study.
Unfortunately, proper differentiation and interpretation of age, period, and cohort effects is not the only challenge in longitudinal research of older adults. Another vexing problem is that of a healthy participation effect, which is a source of bias attributable to the common situation that study participants tend to be healthier, on average, than nonparticipants. This source of bias can lead to a misspecification of the association between predictor variables and outcomes, to restricted variation in predictors and outcomes of interest and their attendant effects on statistical power, and reduce generalizability of study findings. What makes this issue particularly problematic is that the healthy participation effect tends to attenuate over time, perhaps due to the fact that the aging process itself catches up with persons who participate in a study. In other words, a typical 75-year-old person who enrolls in a study (i.e., at baseline) may be quite different, and generally healthier, than an otherwise comparable person who turns 75 after several years of follow-up. In addition, the magnitude of the healthy participation may be correlated with age itself, as it may become more prominent at increasingly older ages. It may therefore not be uncommon to see that age at baseline shows a substantially different association with an outcome of interest (and often considerably weaker in the case of a health outcome) than aging does as it unfolds during follow-up. To state this issue in methodological terms, the cross-sectional age effect may not be equal to the longitudinal age effect.
Cross-Sectional and Longitudinal Age Effects
The most direct and common way to account for potential differences between cross-sectional and longitudinal age effects is to compute separate estimates for each (see, for example, Beckett et al., 1996; Mendes de Leon, Barnes, Bienias, Skarupski, & Evans, 2005). One accomplishes this by modeling age at baseline separately from aging during follow-up or its equivalent, time on study. The apparent disadvantage of this approach is that the longitudinal aging effect, usually the parameter of interest, represents a time-since-baseline effect conditional upon age at baseline, rather than the effect of "time-varying" aging itself. An alternative approach is to reorganize the outcome data by age at any given assessment, as Shaw and colleagues (2007) did, and then model the data as a function of time-varying age. This approach provides a more direct estimate of aging itself, one that is not conditional upon age at baseline, which facilitates interpretation. However, researchers must weigh this advantage against the risk of mixing potentially unequal cross-sectional and longitudinal age effects into one parameter. The extent to which these two age effects differ may lead to a biased estimate of the age effect and, by consequence, the association of a predictor variable of interest on aging-related outcome variables.
It is true that differences in observed aging-related trajectories over time that occur as a function of age at baseline may be indicative of a birth cohort effect. In the context of the article by Shaw and colleagues (2007), this would mean that persons who were born in the 1920s would have experienced different trajectories of change in social outcomes as they aged than persons born in the 1910s or in the 1930s. To account for this, Shaw and colleagues adjusted analyses for birth cohort, defined in 10-year calendar years of birth periods. This adjustment resulted in a change of 40% or more in the magnitude of the (unconditional) age effect for 5 of the 11 social outcome variables compared to the original analysis (not shown in the article). Admittedly, though, it had inferential consequences for only two of the outcomes (ps became >.05). Nonetheless, these findings suggested that birth cohort had a considerable effect on the aging-related trajectories for about half of the outcomes considered in the analysis.
Alternatively, baseline age-dependent differences in observed aging-related trajectories of change over time may be due to a healthy participation effect rather than a cohort effect. This is perhaps a matter of interpretation, and it is difficult to decide conclusively within a particular analysis. However, a healthy participation effect may not manifest itself in discrete 10-year age intervals; it is more likely to show a gradient association with age, becoming increasingly greater at older ages. This, in turn, raises the question whether adjustment in 10-year age groups is sufficient, as such broad age categories may leave ample room for residual variation within each age category associated with the healthy participation effect. Whatever the origin of baseline age-dependent differences in trajectories of change over time, it is usually fairly straightforward to examine this issue in a particular longitudinal data set. A simple method is to conduct an initial analysis modeling the outcome of interest in relation to the cross-sectional (baseline) and longitudinal (time on study) age effects separately to see how similar these two age effects are to each other. How similar is reasonably similar? In the absence of any official criteria of which I am aware, I take the liberty to offer some general guidelines. A difference of less than about 10% between the cross-sectional and longitudinal age coefficients would probably raise little concern, and one could proceed by using time-varying age itself as the time axis for the longitudinal analysis. Differences of about 25% or more might be problematic and probably should be regarded as a red flag when mixing cross-sectional and longitudinal age effects (which is what grouping longitudinal data according to age, rather than time since baseline, essentially does). In between is the gray zone, in which decisions may depend on the absolute effect of age. These guidelines may seem conservative, but that is because there are few compelling reasons not to model cross-sectional and longitudinal age effects separately. After all, there are effective graphical methods to illustrate and interpret aging-related changes on the basis of analytic models using time-on-study as time scale. I have tried to demonstrate this in a recent article on racial differences in disability published in this journal (Mendes de Leon et al., 2005). Precisely because gerontologists' primary theoretical interest is in describing and understanding aging-related change over time, I favor analytic approaches that minimize the potential misspecification of the effect of age itself, even if other approaches appear to be theoretically more informative or appealing.
ANALYZING CAUSES OF AGING-RELATED CHANGE
The Intrinsic Nature of Aging-Related Change
Reflections about the analysis of aging and change over time in the article by Shaw and colleagues (2007) draw attention to another issue that, in my opinion, is equally deserving of more careful consideration in research. In their article, Shaw and colleagues conceptualized the aging effect on social outcomes as a gradual process, and they analyzed their outcome data accordingly. In my view, this is an appropriate choice because it most likely corresponds to the nature of change that occurs as a result of the aging process. This approach contrasts with many other studies that conceptualize and analyze outcomes as a qualitative process, in which outcomes are represented by categorical (usually dichotomous) variables. We do this even if we understand the underlying processes that give rise to these outcomes to be gradual or quantitative in nature. Why do we do this? One reason is that we have a tendency to organize our views of ourselves and the world around us in boxes, in distinct categories. This serves the obvious purpose of facilitating interpretation and communication of the phenomena we discuss with one another. Another important reason is that we may wish to inform clinical practice, which depends on the assignment of heterogeneous outcomes in distinct diagnostic categories to allocate or justify treatment decisions. In other settings, we may wish to address the descriptive purpose of quantifying the size or scope of a particular health or social problem, which is often referred to as the public health impact. We usually do this by estimating the percentage of a given population that meets certain diagnostic criteria that identify the problem. The question is, however, whether the use of categorical outcomes defined by diagnostic or other types of cutoff criteria serves the purpose of etiological research equally well. The problematic nature of dichotomizing variables that represent intrinsically quantitative traits or outcomes have certainly been described before, from both a conceptual and a statistical perspective (Mirowsky & Ross, 1989; Royston, Altman, & Sauerbrei, 2006). In the remainder of this commentary, I hope to offer a simple illustration of the potentially serious but often underrecognized bias that may result from this approach in establishing causal associations between risk factors or predictor variables and outcomes.
It seems reasonable, in my view, to recognize that most phenomena within and around us, including those of particular concern to gerontologists, do not necessarily manifest themselves in clear-cut categories. Instead, they tend to occur along a continuum or a spectrum, in quantitative form. Why? Because most phenomena that change over time tend to do so at different rates or speeds across individuals. Differences in the rate of change are perhaps due to the fact that most outcomes considered in gerontological and geriatric research—such as disability, depression, self-rated health, cognitive function, frailty, to name just a few—are relatively heterogeneous "phenotypes" that are most likely the result of very complex interactions among multiple factors of genetic and environmental origin. Due to variable rates of change, most phenomena or outcomes occur along a spectrum in a population, with individual members ranking at different locations along that spectrum depending on the rate of change they have experienced up to that point (ignoring for the moment the fact that individuals may also differ in initial status achieved, for example, at conception, birth, or at the end of development during childhood). Although individuals may experience random fluctuations in a given outcome that do not follow a particular direction, we concern ourselves primarily with phenomena that are characterized by more or less systematic patterns of change in a population. Gerontological and geriatric outcomes such as those listed previously are driven by aging-related processes and manifest themselves in gradual change over time when measured at the level of the population, even if individual members may show some up and down fluctuations within shorter periods of time.
This basic perspective on the nature of change has important ramifications for the analysis of change, involving two essential requirements. First, researchers need to measure the underlying phenomena with sufficient sensitivity and frequency to determine differences in rate of change. Second, researchers need to analyze the observed changes with sufficient precision to identify the determinants or causes of such changes. Clearly, the first requirement depends on the availability of adequate measures of outcomes of interest and adequate resources to measure them in a sufficiently large sample with sufficient frequency to capture the process of change. The second requirement involves the application of quantitative approaches to the analysis of change. Such approaches are sometimes eschewed, as they may appear to be in conflict with scientists' desire to address "meaningful" change (e.g., for findings to have clinical or public health relevance). To accomplish the latter, researchers reformulate the outcome variables in qualitative terms, in categories, dichotomies, even when they have the quantitative information. Unfortunately, categorization of intrinsically quantitative outcomes can have serious consequences for the results of analyses and the interpretation of findings. A simple example may illustrate this point.
Potential Bias in the Analysis of Change: An Example
A researcher wishes to examine the effect of depression on change in disability, drawing from longitudinal data on disability from a cohort of older adults. Disability in a general population of older adults is probably best seen as a progressive process, driven by various underlying and often comorbidly occurring disease processes that affect humans as they age (Manton, Corder, & Stallard, 1997; Pope & Tarlov, 1991). Progression of disability is potentially modified by a number of psychosocial and environmental characteristics (Verbrugge & Jette, 1994), of which depressive symptoms is a widely studied example. Figures 1 through 3 depict the gradual decline in functional ability (or increase in disability) over time as a function of two levels of depressive symptoms (which, for ease of presentation, I will refer to as high and low depression). Consistent with previous research (Berkman et al., 1986; Ormel et al., 1998), one can assume that there is a cross-sectional (i.e., baseline) association between depression and disability, such that persons with high depression tend to report more disability represented by a lower level of functional ability (the lower of the two lines in each figure). The dashed line at a value of functional ability of 5 marks the (arbitrary) cutoff for a categorical "definition" of disability: Values of 5 and below are indicative of disability; values greater than 5 are indicative of no disability. If the researcher performs an incident type of analysis, in which he tries to identify predictors of disability, he would normally remove all persons with ability values of 5 or less from the analysis, which is why neither of the two lines starts out at that level. However, level of depression would still be associated with the underlying level of ability in the range above 5, even if the assumption were that everyone in that range was nondisabled. In other words, there is a residual correlation between depression and disability among the nondisabled, even if it often remains unmeasured or uncontrolled in incident disability analyses. The three figures present three different types of associations between level of depression and disability; each one would lead to exactly the same conclusion in an incident disability analysis but very different conclusions in a quantitative analysis.
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In Figure 2, depression shows the same baseline or cross-sectional association with disability but a different longitudinal association, with no difference in the rate of functional decline between high and low depression. Such a pattern normally would make researchers reluctant to conclude that depression is causally related to change in disability. In an incident analysis, however, high depression would still reach the cutoff value of 5 earlier than would low depression, and would therefore be associated with increased risk for disability. Thus, dichotomization of the disability outcome variable may result in a biased estimate of the underlying association between depression and disability, and hence lead to a potentially erroneous inference about the casual relationship between depression and disability. Does such a pattern of findings occur in actual studies? Researchers (including myself) have reported significant associations between depression and incident disability (Bruce, Seeman, Merrill, & Blazer, 1994; Cronin-Stubbs et al., 2000; Penninx et al., 1998; Penninx, Leveille, Ferrucci, van Eijk, & Guralnik, 1999), although more detailed quantitative analysis has subsequently cast doubt on the causal nature of this relationship (Everson-Rose et al., 2005; Ormel, Rijsdijk, Sullivan, van Sonderen, & Kempen, 2002).
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). Such patterns may occur, for example, due to a ceiling effect, whereby persons with high social engagement often experience or report very little disability at study entry, hence the usually strong negative cross-sectional association. Over time, however, the force of aging, due to progressively deteriorating health, may overwhelm any presumed protective effect of social engagement on disability such that disability levels among more socially engaged persons will increasingly approximate those among individuals with lower levels of social engagement at baseline.
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CONCLUSION
This commentary was meant to illustrate the potential pitfalls in the analysis of aging-related processes. The tendency to formulate clear and distinct outcome categories that allocate people into separate boxes is a common practice that affects many gerontological and geriatric outcomes. The need to convey the results of studies in readily understandable and potentially translatable clinical or public health terms is clearly very important. There is, parenthetically, no intrinsic reason why this cannot be accomplished using findings from a quantitative analysis, just as I argued for the issue of time scale. The use of diagnostic criteria may inform treatment and intervention decisions to determine who is eligible or might benefit from a certain type of surgery, pharmaceutical therapy, or nursing home admission. The purpose of this commentary is to draw a clear distinction between etiologic research and clinical decision making. In etiologic research, scientists are best served by an approach that corresponds with an understanding of the underlying processes that produce the outcomes that they wish to study. Most of these processes will evolve gradually over time: They do not necessarily behave the same way in cross-section as they do over time, and they do not normally manifest themselves as qualitatively distinct outcomes in the general population. A more accurate analysis of these processes will generate in all likelihood results that show better reproducibility across settings and over time, and ultimately offer the best chance of detecting the actual causal determinants of these processes. This should, in theory, also help researchers identify the most effective treatments and interventions to prevent or reduce the adverse consequences of aging-related declines in health and other important outcomes.
Acknowledgments
This research was supported by Grant ES 10902 from the National Institute of Environmental Health Sciences and Grant AG 11101 from the National Institute on Aging. I am indebted to many of my colleagues with whom I have discussed these issues over the years, and I would like to mention in particular Drs. Denis Evans, David Bennett, Julia Bienias, and Michael Babyak.
Footnotes
Decision Editor: Kenneth F. Ferraro, PhD
Received for publication January 19, 2007. Accepted for publication February 2, 2007.
References
This article has been cited by other articles:
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  B. A. Shaw and L. S. Spokane Examining the Association Between Education Level and Physical Activity Changes During Early Old Age J Aging Health, October 1, 2008; 20(7): 767 - 787. [Abstract] [PDF]
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 B. A. Shaw, N. Krause, J. Liang, and J. Bennett Age Versus Time Since Baseline as the Time Scale in the Analysis of Change J. Gerontol. B. Psychol. Sci. Soc. Sci., May 1, 2007; 62(3): S203 - S204. [Full Text] [PDF]
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