Brain structure and cognitive ability in healthy aging: a review on longitudinal correlated change

GM

The GM volume gradually declines across the adult lifespan (Hedman et al., 2012). However, the onset, and the shape (e.g. linear, quadratic) of tissue loss are dependent on the brain region under study (Ziegler et al., 2012). Cross-sectional estimates of age-differences suggest that the implied decline of GM volume typically follows a last-in-first-out pattern, with anterior brain regions (e.g. prefrontal cortex) being the latest to mature and the first to show age-related deficits, and posterior regions that mature early in development (e.g. visual, auditory cortex) being less vulnerable to GM atrophy (Sowell et al., 2004). This pattern of structural brain differences across age is confirmed by a longitudinal study, with the exception of structures of the medial temporal regions (e.g. hippocampus, amygdala), which showed moderate reductions in children and young adults, but declined substantially in older adults (Tamnes et al., 2013). Regarding the shape of GM change across the adult lifespan, an age-heterogeneous longitudinal study (age range 23–87 years) reported nonlinear (implied) declines over age for GM volume in most areas of the cortex, with accelerating declines in temporal and occipital, and decelerating declines in prefrontal and anterior cingulate regions (Storsve et al., 2014). As cortical thickness and surface area are the two constituent measures of GM volume, those measures were also investigated. Interestingly, larger and nonlinear changes were found for cortical thickness, while surface area showed smaller and predominantly linear curves across most regions of the cortex. The authors interpreted this as evidence that cortical thickness contributes more strongly to GM volume changes in old age than surface area. Measuring middle-aged to older adults for up to five measurement occasions, Rast et al. (2017) reported nonlinear cortical thinning over 8 years in five lobar composites across the cortex, but with decelerating changes, which were most pronounced for older adults in frontal, temporal, and cingulate cortices. With regard to subcortical structures, cross-sectional evidence across multiple sites shows a pattern of age-differences indicative of predominantly nonlinear decline trajectories across chronological age (e.g. hippocampus, caudate), but also of linear decline slopes for some structures (e.g. thalamus, accumbens; Walhovd et al., 2011; Ziegler et al., 2012; Fjell et al., 2013). These findings need to be interpreted with caution, however, as the automated reconstruction of subcortical structures is shown to be of variable reliability, depending, for example, on segmentation choices or the size of the structures (i.e. lower reliability for small structures, Morey et al., 2010).

WM

Cross-sectional estimates of age-differences (Westlye et al., 2010; Liu et al., 2016) and longitudinal estimates of change (e.g. Hedman et al., 2012) suggest that WM volume follows a nonlinear developmental pattern across the adult lifespan, with (implied) increases up to around age 50, and accelerated age-differences or declines thereafter. Similar to GM volume, the onset of WM volume decline is region-specific. The largest age-differences and declines were found in the frontal cortex, succeeded by the temporal (Bartzokis et al., 2001; Raz et al., 2005) and parietal cortices (Resnick et al., 2003), whereas occipital regions remain relatively spared (Raz et al., 2005).

Besides volumetric deficits, WM degradation in the course of healthy aging manifests itself also as age-differences and declines in microstructural properties of WM fiber tracts, and as an accumulation of WMH with increasing age (see Bennett and Madden, 2014 for a review). The former can be estimated with diffusion-weighted MRI (DW-MRI), a MRI method sensitive to the diffusion of water molecules in the brain (Jones, 2010). Compared to nonrestricted diffusion of water molecules (i.e. in a glass of water), diffusion is highly directed in WM with the fibers acting as natural boundaries limiting the diffusion movement in certain directions. Indices derived from a tensor model fitted at each voxel reflect, for example, the degree of directedness of diffusion (fractional anisotropy, FA), or the mean rate of diffusion of a tissue (mean diffusivity, MD), independent of directionality (see Table 1; Beaulieu, 2002). Findings from cross-sectional studies show lower FA and higher MD in older as compared to younger adults (e.g. Cox et al., 2016), which is often interpreted as age-related deficits in the integrity of WM tracts. However, this interpretation is criticized (Jones, 2010), due to the lack of specificity of these measures with regard to their neurobiological foundation (see also Box 1). The few existing longitudinal studies demonstrate changes in WM microstructure with increasing age that are indicative of WM degradation, with prefrontal fiber systems being especially vulnerable to degradation (e.g. Barrick et al., 2010; Sullivan et al., 2010; Teipel et al., 2010). In addition, some longitudinal studies are suggestive of a similar last-in-first out pattern of change as seen in brain volumetric indices (e.g. Bender et al., 2016b; Storsve et al., 2016). However, exceptions to this trend is noted, with larger declines in posterior than frontal regions (Salat et al., 2005), and some support also exists for a superior-inferior gradient of WM aging (e.g. Sexton et al., 2014). Also, studies of WM microstructure in healthy aging increasingly differentiate between diffusion parallel (axial diffusivity; AD) and perpendicular (radial diffusivity; RD) to the main axis (see Table 1). Besides the changes in diffusion properties, increasing age is associated with a higher amount of WMHs, with cross-sectional estimates indicating a linear trajectory (e.g. Birdsill et al., 2014). WMHs can be detected and extracted from T2-weighted MRI images (particularly from pulse sequences; Fluid-Attenuated Inversion Recovery) using manual or (semi)-automated approaches (see Wardlaw et al., 2015) and are linked to pathological changes in vascular functions (Bennett and Madden, 2014). In a longitudinal study with healthy elderly, WMH volume increase was most pronounced in anterior regions of deep WMH (Sachdev et al., 2007).

CSF

Cross-sectional estimates suggest that CSF volume is larger in older compared to younger adults, and the CSF-filled ventricles appear to expand quadratically over the lifespan, with relative stability up to middle adulthood, and accelerated expansion thereafter (DeCarli et al., 2005; Carmichael et al., 2007; Fjell et al., 2013). Ventricular expansion is often used as a nonspecific proxy for global structural brain differences and changes and is shown a sensitive biomarker for AD progression (Madsen et al., 2013).

Whole brain volume

Especially in earlier publications, authors used variables reflecting combinations of tissue classes in order to make conclusions about differences and changes in whole brain volume. Depending on whether CSF is included in these measures or not one can dissociate total brain volume (TBV) from intracranial volume (ICV); (for more details, see Table 1). Some authors also use a measure of TBV that is normalized for some estimate of overall head size (e.g. ICV), hereafter termed as normalized brain volume (NBV). NBV is a widely used index for brain atrophy, as overall head size as measured by ICV remains relatively stable across the lifespan and thus serves as a good measure to reduce between-subject differences with regard to maximum healthy brain size (e.g. Whitwell et al., 2001). A meta-analysis of 22 longitudinal studies implies a gradual decline in whole brain volume of 0.2% per year around the age of 35, and accelerated declines around age 60 (0.5% per year; Hedman et al., 2012). As whole brain volume includes both GM and WM, this estimated trajectory reflects a combination of the latter indices. Consequently, whole brain volume is a rather crude estimate of structural brain changes.

Summary

The mean trends reported above show that age exerts a stronger influence on brain structure in older than younger adults, which is reflected in the dominance of age-differences and decline in healthy old age. Interestingly, the average onset and the shape of age-related structural brain degradation varies depending on the type of tissue and the brain region under investigation, implying regional differences in structural brain aging that are shared among individuals. Roughly, GM atrophy onset is estimated at earlier ages, while WM remains relatively stable until old age. Moreover, a mean trend towards higher vulnerability of anterior, late developing regions as opposed to posterior, early developing regions is reported by several studies of WM and GM aging. A premise of STAC-r is that life course experiences of various kinds shape brain structure besides the mere influence of passing time. Assuming that the brain remains plastic up into higher ages, variability between healthy aging individuals with regard to the onset and shape of brain structure change can be expected (i.e. including maintenance and growth as potential trajectories). The finding of predominantly nonlinear average trajectories for many brain structures (e.g. cortical thickness, subcortical GM, WM) lends some support to this hypothesis.

Intelligence

Five studies observed level-change or correlated change associations of GM with a measure of intelligence (Raz et al., 2008; Ritchie et al., 2015b; Persson et al., 2016; Leong et al., 2017; Yuan et al., 2018). Two very well-powered studies used latent change score models (LCS; McArdle and Hamagami, 2001; McArdle, 2009) to assess correlated changes between latent measures of GM volume and latent measures of cognitive ability (Ritchie et al., 2015b): n=657; Persson et al., 2016: n=167). The LCS model is estimated in the structural equation modeling (SEM) framework and allows the estimation of a latent change score between two subsequent measurement occasions, thus separating true change (at least in part) from measurement error. Furthermore, using the LCS model, it is possible to separate interindividual differences from intraindividual change (for a further explanation of this model, see section ‘The benefits of longitudinal designs’ on latent change models). Ritchie et al. (2015b) found significant correlated changes between GM volume and fluid intelligence, such that steeper declines in GM volume were associated with steeper declines in fluid intelligence over a period of 3 years. Furthermore, Persson et al. (2016) reported that participants with lower baseline GM volume in cerebellar hemispheres, parahippocampal gyrus, and hippocampus showed larger declines in fluid intelligence over 2 years. Also using the LCS model, Raz et al. (2008) found that steeper changes in entorhinal cortex volume were associated with lower levels of fluid intelligence in a sample of young and older adults (age range 20–77). Moreover, Yuan et al. (2018) reported differential effects of fluid and crystallized intelligence on GM aging: while participants with higher fluid intelligence levels demonstrated reduced cortical GM volume shrinkage over a time span of around 5 years, participants with higher levels of crystallized intelligence showed steeper declines in cortical GM volume and total cortical thickness. The authors were, however, unable to compute correlated change, due to a lack of interindividual differences in the cognitive variables. Finally, using a composite of global cognition across five fluid cognitive tasks (i.e. EF, processing speed, verbal, and visuospatial memory), Leong et al. (2017) reported positive correlated changes of this measure with total GM volume (specifically frontal, parietal, and temporal lobar volumes) and hippocampal volume. In contrast, the authors reported negative correlated changes between lobar GM in the occipital cortex and global cognition, indicating that on average, increases in occipital GM were associated with decreases in global cognition.

Memory

The most consistent evidence was found for correlated changes between episodic memory and GM volume or GM thickness in medial temporal regions (Persson et al., 2012; Fjell et al., 2014; Gorbach et al., 2017; Hohman et al., 2017; Leong et al., 2017; Anblagan et al., 2018). With one exception (n=26: Persson et al., 2012), these studies included large (e.g. n=111: Leong et al., 2017) to very large (e.g. n=655: Anblagan et al., 2018) sample sizes.

Two studies could show positive longitudinal associations between hippocampal volume and episodic memory, such that older adults with larger baseline hippocampal volumes (Hohman et al., 2017), or less hippocampal atrophy over time (Leong et al., 2017) showed less declines in episodic memory over a period of 4–8 years, respectively. Furthermore, Persson et al. (2012) reported that changes in episodic memory were positively correlated with changes in the right hippocampus, as well as hippocampal volume at follow-up (after 6–10 years) in a sample of middle-aged to older healthy participants. Similarly, Gorbach et al. (2017) found positive correlations between 15-year changes in an episodic memory composite of five tasks and simultaneous 4-year changes (towards the end of the same testing period) in GM volume of the hippocampus in a sample of healthy middle-aged to older adults. Notably, this effect was driven by the participants aged over 65. To reduce practice effects, the authors used slightly different versions of the episodic memory tasks across measurement occasions (i.e. by switching item lists between tasks or changing the item order). Also, one study found that baseline hippocampal microstructure as measured with MD (more conventionally used to detect WM changes; see Table 1), was associated with changes in verbal episodic memory (Anblagan et al., 2018), such that participants with higher MD showed steeper subsequent declines in episodic memory performance. In contrast, correlated changes between hippocampal volume and verbal episodic memory did not survive correction for multiple comparisons. The authors speculate that higher MD values might reflect an age-related increase in water content in hippocampal tissue that could be a precursor for age-related pathological changes that influence cognitive abilities before brain atrophy can be observed (Anblagan et al., 2018).

Positive correlated changes with episodic memory were also reported for cortical thickness in the entorhinal cortex (Fjell et al., 2014) and in right hemispheric regions (Sala-Llonch et al., 2014; Möller et al., 2016). Finally, one study reported a significant association of higher baseline episodic memory performance with reduced 2-year GM volume declines in the lateral prefrontal cortex in a sample including younger and older adults (age span of 19–79 years; Persson et al., 2016).

EF

Four studies reported level-change associations for a measure of GM and EF: in a large sample of healthy controls of the Alzheimer’s disease and neuroimaging initiative (ADNI; n=379), baseline hippocampal volume was positively related to changes in EF over 4 years (Hohman et al., 2017), suggesting that older adults with lower hippocampal volume showed steeper declines in EF. Similarly, Leong et al. (2017) reported positive correlated changes between hippocampal volume and EF over 8 years of follow-up. In addition, in one study, 2-year changes in cortical thickness of the right occipital cortex were negatively correlated with simultaneous performance changes in EF tasks (Möller et al., 2016).

Working memory

Only one study found longitudinal relationships between hippocampal MD and working memory (Anblagan et al., 2018): unlike the level-change association, which went into the expected direction, correlated changes between MD and working memory were positive, suggesting that increases in MD (usually interpreted as disruptions in WM microstructure) were related to improvements in working memory. However, due to the lack of specificity of MD, other influences (e.g. crossing fibers) could potentially have led to a local increase in MD (Zatorre et al., 2012).

Processing speed

In two well-powered studies using data from the Lothian Birth cohort, more intact hippocampal GM at baseline (i.e. lower MD; Anblagan et al., 2018), and less decline in whole brain GM volume (Ritchie et al., 2015b) were associated with reduced declines in a latent measure of processing speed over 3 years.

However, nine studies did not show any longitudinal relationships between GM and cognition regarding correlated change (Cohen et al., 2001; Raz et al., 2007; Daugherty et al., 2015; Mak et al., 2015b; Fjell et al., 2016; Persson et al., 2016; Hohman et al., 2017), level-change (Ritchie et al., 2015b) or both (Leow et al., 2009). Several of these studies had comparatively small sample sizes (between n=25 and 56) and might have thus not been sufficiently powered to detect any significant effects (Cohen et al., 2001; Raz et al., 2007; Leow et al., 2009; Mak et al., 2015b; Fjell et al., 2016).

Intelligence

Several studies found positive level-change or correlated change associations between global measures of WM health and some measure of fluid intelligence, such that lower baseline WM volumes or faster degradation of WM were associated with larger declines in intelligence performance. Specifically, accumulation of global WMH volume over time (Schmidt et al., 2005; Raz et al., 2007; Ritchie et al., 2015b), decrease in global FA (Ritchie et al., 2015a), and both lower baseline prefrontal WM volume and atrophy therein (Persson et al., 2016) were associated with declines in intelligence over time. These studies all covered a time span between 2 and 6 years. Furthermore, several of these studies used LCS models to investigate interindividual differences in intraindividual changes (Ritchie et al., 2015a),b; Persson et al., 2016), and included large to very large sample sizes given the standards in the field (n=731: Ritchie et al., 2015a; n=657: Ritchie et al., 2015b; n=167: Persson et al., 2016).

Memory

Some evidence also exists for correlated change associations between WM health and measures of episodic memory (Schmidt et al., 2005; Silbert et al., 2008; Ritchie et al., 2015b; Fjell et al., 2016; Bender et al., 2016a; Leong et al., 2017). In one study, larger declines in global and lobar (i.e. parietal and frontal) WM volume were related to steeper declines in a composite reflecting verbal episodic memory performance (Leong et al., 2017). Furthermore, three studies reported negative correlated changes between WMH and episodic memory (global WMH: Schmidt et al., 2005; subcortical WMH: Silbert et al., 2008; global WMH: Ritchie et al., 2015b), which can be interpreted as a positive relationship between changes in WM health and episodic memory. Also, one study reported a relationship between changes in WM microstructure (increases in MD of the cingulate gyrus) typically understood as WM deterioration, and declines in episodic memory (Fjell et al., 2016). However, Bender et al. (2016a) observed the opposite relationship. In their study, changes in WM microstructure (decreases in FA, increases in RD), which are commonly interpreted as WM degradation were correlated with improvements in episodic memory. Given the uncertainty regarding the cellular mechanisms of change in diffusion properties, however, it is also possible that the pattern of WM changes reflects a form of plastic reorganization (Bender et al., 2016a).

EF

Two studies reported evidence for level-change or correlated change associations between WM and EF (Fjell et al., 2017; Moon et al., 2017). Fjell et al. (2017) found a negative correlation between MD changes in the inferior and superior longitudinal fasciculi (averaged across hemispheres) with performance changes in a shifting condition of the stroop task across a period of 3 years. However, the result for the superior longitudinal fasciculus did not survive control for age. This means that increases in MD in the inferior longitudinal fasciculus were related to declines in inhibitory control, independent of participant age. In a subsample of cognitively healthy elderly, Moon et al. (2017) reported a negative association between WMH progression and steeper 3-year declines in EF, measured as performance in the Trail Making Test B. This relationship was not found for the entire sample, which contained also participants with impaired cognition (i.e. clinical dementia rating scale>0).

Working memory

One study reported negative correlated changes between a measure of WM microstructure (i.e. MD; higher values reflect lower integrity) and a composite of two working memory tasks (Charlton et al., 2010). These tasks are elsewhere interpreted as measures of fluid intelligence (Ritchie et al., 2015a),b).

Processing speed

Overall, five studies found level-change or correlated change associations between WM health and processing speed. Notably, these studies were very well-powered, with sample sizes above n=400 (with the exception of Moon et al., 2017). Based on participants from the same sample of healthy older adults, two studies reported positive correlated changes over 2 years between indices of WM microstructure (decreases in FA, increases in MD) of the corticospinal tract and processing speed (Lövdén et al., 2014; Köhncke et al., 2016), indicating that older adults with less intact WM microstructure in the corticospinal tract show steeper declines in processing speed. Furthermore, lower baseline global FA (Ritchie et al., 2015a), higher global WMH at baseline, and higher WMH increases were associated with steeper declines in processing speed (Ritchie et al., 2015b; Moon et al., 2017).

Finally, seven studies did not show any longitudinal relationships between WM and cognition regarding correlated changes (Schmidt et al., 1999; Gorbach et al., 2017), level-change associations (Raz et al., 2008; Silbert et al., 2008; Charlton et al., 2010; Bender et al., 2016a), or both (Song et al., 2018). The sample sizes of these studies were very heterogeneous, with some including smaller (e.g. n=84: Charlton et al., 2010; n=55: Song et al., 2018), and others large samples of more than 200 participants (Schmidt et al., 1999, 2005; Gorbach et al., 2017).

Memory

Three studies found positive level-change (Ritchie et al., 2015b) or correlated change associations (Schmidt et al., 2005; Leong et al., 2017) of a measure of episodic memory and of a measure of whole brain volume (see Table 1), in the direction that participants with lower levels of episodic memory performance at baseline, or decreases therein, showed on average steeper decline in whole brain volume. These studies were well to very well-powered (n=329: Schmidt et al., 2005; n=657: Ritchie et al., 2015b; n=111: Leong et al., 2017).

With regard to CSF, two studies found negative correlated change associations between ventricular volume and episodic memory performance, such that ventricular enlargement (CSF increases) was related to simultaneous or subsequent declines in memory performance (Grimm et al., 2012; Leong et al., 2017). Specifically, we would like to highlight the study by Grimm et al. (2012), which was the only one to model lagged correlated changes. The authors assessed 149 participants in a measure of CSF (lateral ventricle volume) and episodic memory with seven repeated measurements over a maximum period of 10 years. They estimated change across participant age (60–90 years) in a bivariate dual change score model (a variant of a LCS model). Conducting a series of model comparisons, they concluded that a final model where previous changes in CSF led to subsequent changes in episodic memory reflected the data best, whereas the other directionality (cognitive changes leading to brain changes) lowered model fit substantially. We would like to emphasize this study, as it provides the methodological tools to explore directional hypotheses in the study of dynamic within-person associations between changes in brain structure and cognitive ability. As the expansion of CSF in the ventricles indicates a loss of brain volume, these results, when taken together, mirror the findings for whole brain volume.

Other

In addition, Schmidt et al. (2005) reported positive correlated changes of NBV with a composite of four cognitive tasks that tap into attention and processing speed. Another study reported a negative association of ventricular expansion with executive function declines (Leong et al., 2017).

However, two studies did not find any significant association regarding level-change and correlated change associations (Charlton et al., 2010; Mak et al., 2017). These studies had smaller sample sizes compared to the studies reported above that found significant brain structure-cognition relations (i.e. n=106: Charlton et al., 2010; n=33: Mak et al., 2017), thus having less power to detect any significant effects.

Summary

In conclusion, so far only a small number of studies have investigated level-change or correlated change associations between measures of brain structure and cognitive ability. Several of these studies report positive associations, indicating that declines (or increases) in structural brain intactness are related to simultaneous losses (or gains) in cognitive performance. However, others have found the opposite relation, such that brain structure was negatively associated with cognitive ability, or showed no significant correlation at all. In light of the scarcity of evidence, the positive association between structural brain properties of medial temporal regions (specifically the hippocampus) and global brain metrics with episodic memory has received comparatively more attention. As the hippocampus is involved in neurogenesis up into old age (Lillard and Erisir, 2011), this structure is highly relevant for brain plasticity, and potentially also for compensatory scaffolding (see also Park and Reuter-Lorenz, 2009). We also found some support for level-change or correlated changes of global GM and WM indices with fluid intelligence, and a few studies showed brain structure relations with EF and processing speed, however, these findings are more heterogeneous. Generally, the interpretation of significant correlated change associations between structural brain indices and cognitive abilities poses a challenge, as it is impossible to disentangle whether age-related neuroanatomical changes are causally linked to simultaneous cognitive declines, or whether a (positive) relationship between these variables reflects a common, underlying causal mechanism. Based on STAC-r, we expected associations between brain structure and cognitive ability to be weak especially in healthy older adults as they should be able to compensate for age-related brain atrophy and thus maintain cognitive performance. Unfortunately, it was not possible to derive a fully comparable measure of the strength of the correlated change relationships, due to large methodological differences between studies. Even if it was possible to gain an effect size estimate, it would be impossible to judge at the present moment if weak brain structure-cognition relationships resulted from methodological limitations of the reviewed studies or actually from intraindividual compensatory resources as predicted by STAC-r. We therefore conclude that the current limitations of the reviewed literature prohibit general conclusions on correlated change relationships in healthy aging. In the following sections, we will discuss these limitations in-depth, and provide ideas for the advancement of methods and theories in the field.

Reliability, shape, and dynamics of change

The majority of the reviewed studies assessed only two measurement occasions. However, two-occasion studies are limited with regard to the reliability of the change estimate (Willett, 1989). A line drawn through two observations will always fit perfectly and hence measurement error will be ignored (King et al., 2018). Consequently, the reliability of the change estimate in two-occasion studies is highly dependent on the accuracy of the individual brain or cognitive measures observed at each occasion (see the sections on reliability and validity of structural brain measures/cognitive ability measures below). Regarding the shape of change, two-occasion studies allow only the estimation of linear change. Ideally, at least four occasions are required to estimate nonlinear trajectories of change (King et al., 2018). As already touched upon in the beginning of this article, cross-sectional and longitudinal evidence supports nonlinear age-related changes in brain structure and cognitive ability. Furthermore, only with more than two measurement occasions it is possible to study time-lagged relations between changes in two variables, and thus test directional hypotheses of the dynamics between structural brain and cognitive changes. It is reasonable to assume that changes in two developmental variables are not perfectly synchronized, but rather follow a lagged pattern, potentially even with bidirectional relations (Salthouse, 2011). Only few studies included three or more measurement occasions (Schmidt et al., 2005; Silbert et al., 2008; Grimm et al., 2012; Gorbach et al., 2017; Leong et al., 2017; Moon et al., 2017; Yuan et al., 2018) that would allow the estimation of more complex change dynamics. Of these studies, all assumed linear curves to estimate correlated change, and only two studies specifically tested first if a nonlinear trajectory fit the data better (which it did not; Hohman et al., 2017; Leong et al., 2017). Furthermore, only one study estimated lagged change relations, using, however, a rough measure of global brain structure changes (lateral ventricle size; Grimm et al., 2012).

Choice of age-range

The samples used in the reviewed studies differed substantially regarding the age ranges covered. Several studies selected a lifespan approach, covering a broad age range from young or middle adulthood to old age. Such lifespan samples are useful for research, as they can inform about development across a longer time span that would otherwise be almost impossible to gather from following one cohort across the entire lifespan. However, one needs to be careful when comparing results of age-heterogeneous studies to those from studies with more narrow age ranges. In age-heterogeneous studies, average change is composed of both within-person change and between-person age-differences. This can be problematic if these two types of age effects do not converge. Age convergence can be formally tested for (Sliwinski et al., 2010), however, it is often not realistic to find age convergence in studies with broad age ranges, as very different developmental mechanisms might be at work in adults of different ages. For example, the chance of experiencing declines in structural brain features and cognitive performance is much higher around age 70 than age 50, and negligibly small for adults in their twenties. Thus, if these two sources of variance are not properly distinguished, estimated rates of change can be confounded with an increased probability of change with age at the between-person level (Hofer and Sliwinski, 2001). Different methodological approaches exist to include between-person age differences better into the analysis. For example, participant’s baseline age can be included as a predictor to control for between-person age differences (see Sliwinski et al., 2010 for an extended discussion).

Definition of healthy aging

As already touched upon in the introduction of this article, healthy aging is not a well-defined term. The current definition of healthy aging provided by the WHO places importance on the interplay between a person’s resources (i.e. intrinsic capacity) and the living context on the micro to macro level that is necessary to retain satisfactory levels of well-being through the successful pursuit of one’s personal goals. This definition of healthy aging is more inclusive than the more general definition of health as a state of ‘complete physical, mental, and social well-being and not merely the absence of disease or infirmity’ (WHO, 1946). The recent definition from the First World Report on Ageing and Health (WHO, 2015) states that healthy aging is a process that applies to individuals at varying levels of functional capacity and health.

Given that the current review focuses on the association between brain and cognition, and that cognitive health is an important predictor of well-being in old age, we understand healthy aging from a cognitive ability point of view. Thus, when using the term healthy aging, we mean aging in the absence of clinically relevant cognitive impairment. All of the studies reviewed here tested for cognitive impairment using one or more common screening instruments for dementia or psychiatric illness related to cognitive impairment (i.e. depression) or described their participants as cognitively normal or dementia-free without closer information on specific instruments or cut-offs used (see column ‘Healthy cognitive aging’ in Tables 2–4). However, they showed vast differences regarding the exact protocols used to determine cognitive health (e.g. medical screening by trained experts vs. brief health interview), and the level of detail they provided in describing these protocols, which is why we direct interested readers to the original publications for more information. Many studies used the same instruments to screen for cognitive impairment (e.g. MMSE; Folstein et al., 1975), lending to some comparability. However, the cut-off values for healthy cognitive aging varied substantially between studies (e.g. from a minimum score of 24 up to a score of 28 in the MMSE). Moreover, many studies applied additional exclusion criteria beyond cognitive health [e.g. diabetes, cardiovascular disease, or vascular risk (VR)], leading to substantial differences in the overall health status between study samples. For example, besides screening for a range of medical conditions (including neurological disorders such as AD), Möller et al. (2016) excluded participants with cerebrovascular disease. In contrast, Raz et al., specifically included a subsample of participants with medically treated hypertension, as they were interested in the effect of VR on brain and cognitive health (Raz et al., 2007, 2008). The choice of criteria influences the prevalence of people categorized as healthy agers substantially (McLaughlin et al., 2012; Rodriguez-Laso et al., 2018). This discrepancy in the use of screening instruments and cut-off criteria underlines the urgent need for a clear consensus on a definition of healthy aging. Finally, on a conceptual level, it is still a matter of debate whether cognitive decline is a normal aspect of healthy aging and disease represents a qualitatively different state of the brain or whether it simply reflects the starting point on a continuum to later disease progression (i.e. dementia) – and age serves as a proxy for pathological changes.

Choice of time interval

The time intervals between measurement occasions varied between studies, ranging from 1 year (Leow et al., 2009; Grimm et al., 2012; Fjell et al., 2014; Mak et al., 2015a,b) up to 15 years (Gorbach et al., 2017). Also, for some studies the time intervals were different for the MRI and cognitive measurements (e.g. Fjell et al., 2014; Gorbach et al., 2017). Depending on the width of the time window under investigation, it is possible that changes are driven by different developmental processes or external influences (Hofer and Piccinin, 2009). When planning a longitudinal study, researchers need to be aware that different neuroanatomical substrates (e.g. volumetric or surface-based measures, WMH, WM microstructure), or different regional structures most likely vary with regard to the timing and duration of age-related change processes. Thus, especially if neuroanatomical measurements are also combined with cognitive performance assessments, there will probably not be any ideal time interval that is suited to capture all of these change processes. Importantly, the choice of the length of the time intervals substantially influences the magnitude of the parameters estimated in traditional statistical models for the analysis of longitudinal data (Voelkle and Oud, 2013). Unfortunately, not many guidelines exist that help researchers in choosing the optimal spacing between measurements when planning a longitudinal study of aging (Dormann and Griffin, 2015).

Choice of covariates

Many authors included one or more covariates into their statistical analysis, to control for the potentially confounding influence of third variables on the relationship between changes in brain structure and cognitive performance (see column ‘Covariates’ in Table 2). Notably, the selection of covariates was heterogeneous between studies, further preventing direct comparisons of the level-change and correlated change relations. For example, while some authors controlled for age only, others additionally included other covariates (e.g. VR, apolipoprotein E allele 4) to control for the impact of neurally depleting factors. A source of heterogeneity was also introduced by different approaches to control for brain size. While some authors decided to adjust the raw brain volumes with a measure of maximum healthy brain size such as ICV (e.g. Persson et al., 2016), others included it as a covariate (e.g. Leong et al., 2017). At the present moment, no clear consensus is reached on one approach in the literature, as many factors play a role (e.g. the measure of brain size: Jäncke et al., 2015), and it is yet unclear how the correction with a global measure of brain size impacts findings in longitudinal developmental studies (Mills and Tamnes, 2014). We acknowledge that the choice of covariates is not a trivial matter, and often neglected in the discussion of results. Furthermore, covariates are often selected retrospectively, based on the variables that are available in a dataset, and not necessarily based on the most relevant potential confounds. This is especially an issue when using large, publicly available datasets that might not be designed for the research question at hand. Even in an ideal scenario where all potential confounds are observed, the decision on which variables to include into an analysis still remains subjective. Importantly, the choice of covariates can substantially alter the results of an analysis, as is nicely demonstrated in a recent study by Silberzahn et al. (2018). They asked 29 teams of researchers to independently analyze the same dataset and answer the question, whether soccer referees are more likely to give red cards to dark skinned players. The conclusions the researchers made varied immensely, in part because of their choice of covariates. Especially with regard to observational studies, the inclusion of certain types of covariates can impose a threat to causal conclusions (see Rohrer, 2018). To enable future meta-analytical comparisons, we thus advocate the transparent reporting of the results both with and without the included covariates. In addition, future studies might consider including time-varying covariates in their analyses, if theoretical reasons exist that they impact brain and/or cognitive performance differentially over time. For example, high body mass index or hypertension is associated to higher risks of developing dementia if experienced in midlife (Kennelly et al., 2009; Kivimäki et al., 2018).

Statistical method

Another source of variation between studies relates to the statistical methods used to model correlated change associations. In most cases, the investigators decided to compute two change scores (raw difference score or a change ratio) and either run a standard correlation between them, or include one score as a predictor and the other as a dependent variable in a regression model (see column ‘Statistical method’ in Tables 2–4). In contrast to a raw difference score, a change ratio is typically standardized with regard to baseline values of brain structure or cognitive ability, thus reflecting a relative difference. As many authors used different methods to compute change ratios (e.g. annual percentage change vs. the proportion of level at T2 to level at T1), this lack of consensus introduces another source of noise complicating the comparability of previous findings. Irrelevant of the computation, however, change scores include not only variation due to change within individuals over time but they are also confounded by variation stemming from between-person differences. Importantly, the main interest of every investigation of brain structure-cognition relations is to make assertions on how the two variables of interest are related to each other within individuals. Thus, appropriate statistical methods for the analysis of longitudinal change are necessary that are able to isolate these different portions of variance. Such methods are, for example, variants of latent growth curve models (i.e. random coefficient or multilevel models) (Raudenbush and Bryk, 2002), or latent change models (McArdle and Hamagami, 2001; McArdle, 2009), which allow to estimate interindividual (i.e. between-person) differences in intraindividual (i.e. within-person) change. Specifically, a variant of latent change modeling, the bivariate LCS model estimated in a SEM framework is well-suited to address questions of correlated change associations between two variables (Kievit et al., 2018); for more details on the method see section ‘The benefits of longitudinal designs’). Several of the reviewed publications have already adopted this approach (Raz et al., 2008; Grimm et al., 2012; Lövdén et al., 2014; Daugherty et al., 2015; Ritchie et al., 2015a,b; Köhncke et al., 2016; Bender et al., 2016a; Persson et al., 2016; Anblagan et al., 2018).

Power to detect change

The sample sizes studied were highly diverse between studies. Especially, to detect correlated change, sufficient statistical power is necessary. While this is not usually a concern for moderately sized longitudinal studies covering a few years, power can be an issue for short-term longitudinal studies with few measurement occasions, few participants and small effect sizes (cf., Rast and Hofer, 2014). Generally, in order to investigate developmental change in both, cognitive abilities and brain structure, studies will need to cover years rather than months to provide robust estimates of (correlated) change (von Oertzen and Brandmaier, 2013).

Problem of multiple comparisons

Especially in the field of neuroimaging, many statistical tests are often conducted concurrently (e.g. for voxel-wise comparisons across the brain). Specifically, as in the case of the studies reviewed here, when testing hypotheses about correlated changes between different regions of the brain and multiple cognitive abilities, the number of simultaneous hypothesis tests is high, leading to an increased risk of making a type I error (Lindquist and Mejia, 2015). Some authors solved this problem by applying a correction for multiple comparisons (Lövdén et al., 2014); Persson et al., 2014, 2016; Ritchie et al., 2015b; Fjell et al., 2017; Gorbach et al., 2017). Such corrections typically lower the threshold of the p-value, which lowers the risk of false positive results, however, on the downside also leads to a reduction of the statistical power to find the effect of interest (e.g. correlated change). Different methods for dealing with multiple comparisons exist that are designed to keep the loss in statistical power to a minimum (see Lindquist and Mejia, 2015 for an overview). Another possibility in the current context is to use advanced multivariate statistical methods that are able to run multiple hypothesis tests in one model (see section ‘The benefits of longitudinal designs’). In any case, we consider it of high importance to report the applied procedure transparently, and ideally results both with and without corrections for multiple comparisons, as was done, for example, by Ritchie et al. (2015b).

Reuse of data

Several of the reviewed publications use the same sample, or a subsample of the larger participant pool, to address different research questions. Conducting large-scale longitudinal studies requires a lot of time and resources and we strongly agree that it is important to pool efforts and use the collected data in a sustainable and efficient manner. However, it would be desirable to openly communicate this matter and to explicitly address the statistical consequences of using data from the same sample to answer different research questions. We therefore advocate the transparent documentation of the publications that have used data from the same longitudinal database, for example, via an open science platform, such as the Open Science Framework (Foster and Deardorff, 2017).

Reliability and validity of structural brain measures

Another limitation relates to the reliability and validity of indices derived from brain imaging. First, the protocols used to process longitudinal brain imaging data vary greatly between research groups. Whereas some groups use manual or semi-automated methods to delineate anatomical regions of interest, others rely on fully automated procedures. Some use default settings and others additionally apply fine-tuning to such default protocol parameters. This variety introduces unwanted noise into any efforts of replication (Mills and Tamnes, 2014).

An important topic for longitudinal investigations is the concern of retest-reliability. Generally, the measurement of compartmental volumes, surface area and cortical thickness with automated methods is reliable across repeated testing (Vijayakumar et al., 2017), with regional scan-rescan reliabilities ranging between 0.8 and 0.9 (Liem et al., 2015). However, factors such as the measured structure (Morey et al., 2010), choice of segmentation software and protocol (Jovicich et al., 2013; Heinen et al., 2016), or magnetic field strength (Heinen et al., 2016) can impact the reliability. With regard to the assessment of brain structure-cognition relationships, Dickerson et al. (2008) reported reliable estimation of cortical thickness correlates of cognitive performance across different sessions, scanners, and field strengths in a group of healthy older adults. In comparison, measurements from DW-MRI are less robust, with estimated scan-rescan reliabilities between 0.5 and 0.8 in dependence of preprocessing choices and WM measure of interest (cf., Madhyastha et al., 2014). As DW-MRI registers signal-loss due to the movement of water-molecules, the sensitivity to detect changes is specifically affected by head motion artifacts (Yendiki et al., 2014). Even though to a lesser extent, head motion has also been reported to bias estimates of cortical thickness and GM compartmental volumes (Reuter et al., 2015; Alexander-Bloch et al., 2016; Pardoe et al., 2016; Savalia et al., 2017). Especially in longitudinal studies, artefacts such as head motion or changes in scanning systems across occasions (e.g. from field strength 1.5–3T) can increase measurement error and substantially reduce the sensitivity to detect change. To diminish the impact of measurement error when aligning multiple occasion imaging data in three-dimensional space, longitudinal imaging pipelines are now emerging that are designed to re-align the brain images within participants over time (e.g. Reuter et al., 2012; Yendiki et al., 2016). However, only limited evidence is available on how these processing streams perform in the case of long-term longitudinal studies (Willis et al., 2013). Simulation studies would help to shed light on the conditions under which longitudinal processing streams perform optimally or result in an underestimation of change.

Regarding the validity of the brain structure indices with regard to the underlying biological basis, all studies suffer from the same limitation that structural brain measurements from MRI are only estimates of the underlying cellular structure (see Box 1). Furthermore, most of the reviewed studies correlated individual brain measures (either local or global structural indices) with one or more cognitive measures. However, cognitive abilities are most likely based on distinct and distributed brain networks. Thus, a single regional brain measure may capture only a fraction of the variance of the underlying cognitive ability of interest. Another limitation is that single structural brain measurements are often biased by noise. One solution to reduce measurement error and thus to increase the validity of the assessed construct is the use of latent variables to capture the shared variance across multiple brain measures (Kievit et al., 2018). Using such a latent approach, it is also possible to separate more brain-wide effects of aging, which are shared among different structural brain measures from measurement-specific changes (for an example, see Lövdén et al., 2014; Ritchie et al., 2015a,b; Bender et al., 2016a).

Quality control procedures

The reporting and application of quality control procedures was very heterogeneous across the studies reviewed here. This is not surprising, as no consensus exists on standardized procedures for the control of head motion (but see: Yendiki et al., 2016), or quality of the MR images in general (see Vijayakumar et al., 2017, for a review). While there exist many metrics that quantify image quality and can be calculated with tools like QAP (Quality Assessment Protocol, Shehzad et al., 2015) or MRIQC (MRI Quality Control tool, Esteban et al., 2017), determining which metrics provide a good judgment of image quality is nontrivial. Rosen et al. (2018) have recently proposed the Euler number as a metric for the quality of surface reconstruction. Importantly for the fields of development and aging, they demonstrated in a young sample that scan quality mediated the relationship between age and cortical thickness. Furthermore, Esteban et al. (2017) proposed an automatic prediction of an image quality label. However, further work is needed in order to derive quality control standards for those measures.

Reliability and validity of cognitive ability measures

Regarding the assessment of cognitive ability, similar challenges can be discussed that threaten the reliability and validity of repeated assessments. It is well known that in longitudinal studies, practice effects can lead to the underestimation of age-related decline and thus negatively impact reliability (Hertzog and Nesselroade, 2003). One intuitive solution to deal with this problem is to use longer time intervals. However, this might not match the theoretical question at hand. In addition, Salthouse et al. (2004) showed that very long time intervals are required (between 7 and 13 years) until practice effects are no longer observable. Other possibilities are the inclusion of a new subsample at each wave to estimate the performance gains due to repeated testing, or the administration of parallel task versions. Also, estimates of long-term longitudinal change in a cognitive test can be compared to performance gains in a control condition where a subset of the same sample or a different group of individuals complete the same test repeatedly over a short time interval (Tucker-Drob and Salthouse, 2008). Furthermore, practice effects can be explicitly included in the statistical model, if the time intervals between measurements are not confounded with age (see Ferrer et al., 2004).

Regarding the validity of the cognitive measurements, the reviewed studies differ substantially with regard to the assessment of the ability of interest. Whereas some investigators tested associations between brain structure indices and single tasks, others created composites, or latent variables of multiple tasks. The advantage of using multiple tasks is that the problem of task-impurity can be lowered (Miyake and Friedman, 2012). Specifically, estimating latent factors of cognitive abilities with multiple indicators has the advantage of extracting their shared variance, which is free from task-specific measurement error. Another source of variance between studies was the choice of the type of tasks that were used as indicators of a respective cognitive domain. Due to the aforementioned problem of task-impurity, it is often not possible to clearly assign a cognitive task to a specific cognitive ability. For example, whereas one study used the digit span backwards and the letter-number sequencing task as indices for a latent factor of fluid intelligence (Ritchie et al., 2015a), another study combined the same tasks into a composite of working memory (Charlton et al., 2010). As many tasks assessing working memory resemble those measuring some aspect of fluid intelligence (Salthouse and Pink, 2008), both methods are defendable, however. Especially tasks developed in the field of neuropsychology, as were used by many of the reviewed studies, are designed to assess multiple aspects of cognitive abilities (Snyder et al., 2015). For example, the verbal fluency task (i.e. list words of a semantic category or a given starting letter), taps into verbal ability, as well as aspects of executive function (shifting between word clusters, inhibiting nonrelevant words).

In general, we note that the lack of common standards for the assessment of cognitive ability in older age is a major reason for inconsistencies in the results of brain-behavior correlations.

Study design and power to detect change

Attention to study design (i.e. number and temporal spacing of assessments) and measurement-related issues (i.e. reliability, number of indicators, measurement modeling) are fundamental to life course and lifespan developmental research and will have direct influence on the type and quality of results obtained from a research study. Given the extensive costs associated with longitudinal research, especially when neuroimaging is involved, we need to be able to make informed decisions about our designs beforehand in order to get sufficient statistical power with minimal requirements. As such it is imperative to understand what design elements increase statistical power while keeping participant burden, sample size, and measurement occasions minimal without compromising the quality of the data.

Longitudinal studies vary in a number of elements (Lerner et al., 2009; von Oertzen and Brandmaier, 2013; Rast and Hofer, 2014) such as differences in samples (e.g. age homogeneous vs. age heterogeneous; representativeness), number of occasions (e.g. few, many), spacing between assessments (e.g. widely spaced panel designs; single session repeated testing experiment), and whether new samples of individuals are obtained at subsequent measurement occasions (e.g. sequential designs). Moreover, depending on the questions of interest, individuals can be drawn from different populations of birth cohorts, cultures, and nations, born at different historical periods, with short-term or long-term intervals between assessments, and with measures that are time-invariant or time varying within individuals. These features can be combined in a number of ways to create study designs that are particularly suitable for answering research questions that vary in scope from regarding population change across birth cohorts to focusing on the dynamics of short-term within-person processes.

Once the type and expected temporal trajectory of the change process of interest is identified, the longitudinal study needs to be designed accordingly. Assuming that the effect sizes of the phenomenon (e.g. covariance among cortical thinning and cognitive decline) are given in the population and cannot be modified experimentally, researchers typically only have control over the duration of the study, the number and spacing of measurement occasions, and the number of participants that enter the study. These decisions can be optimized in terms of detecting individual differences in change and correlations among change processes. Rast and Hofer (2014), for example, illustrate the interplay among study duration, number of measurement occasions and interval lengths among measurements for statistical power to detect (co)variances of rates of change. Importantly, they showed how statistical power differentially reacts to changes of the study design – these changes can be exploited to optimize the study design. For example, power can be maximized if measurement occasions are spaced out unequally towards the beginning and the end of a longitudinal study. While these decisions can optimize power in general, they should not replace a tailored analysis to investigate what the exact data requirements are for a specific research question and what precautions need to be taken, especially to get the most out of studies in early stages. While Monte Carlo simulations are the most flexible tool as they can recreate the conditions, which our modeling assumption ultimately will be based on, they can also be rather complex. To mitigate the complexity of designing a power analysis and to obtain a ‘feeling’ of how study ingredients are interrelated, Brandmaier et al. (2015) developed the LIFESPAN tool for that specific purpose, which builds on the notion of power equivalence to analytically, and immediately, derive power for different parameter and design combinations (von Oertzen, 2010).

Statistical models

A variety of statistical approaches can be used for the estimation of change and the interaction of change processes in brain structures and cognitive abilities. From our perspective, regression models that have often been used in the past do not adequately capture the between-person variability that is present in datasets of healthy older adults. The multilevel approach and the SEM approach are well suited to model this important aspect. Both approaches contain different techniques, which focus on different modeling aspects. For example, a distinction might be drawn according to the number of dependent variables present in the model (univariate vs. multivariate). Also, models can be divided into ‘static’ and ‘dynamic’ models for change. While static models capture the change process in terms of a given functional form, such as a slope or a nonlinear trajectory, dynamic models follow the tradition of dynamical systems where the focus is on the dynamics underlying the change process itself. While the focus of multilevel approaches is mainly on the measurement model, that is, on the link between observed and latent variables, the SEM approach focuses on the structural models that links the latent constructs to additional covariates or to each other. There is no clear distinction between the two different classes of models, as they can be made equivalent for the most part, but they tend to be applied in different fields and as a result, they have approached longitudinal data from different perspectives.

Univariate multilevel models

A rather simple representation of such an approach and a common analytic method for the analysis of longitudinal data is the technique of latent growth curve modeling (i.e. random coefficient or multilevel modeling). Repeated measurement designs yield at least two levels of analysis: the Level 1 model summarizes individual level outcome data at three or more occasions in terms of ‘true’ initial level of performance (intercept), slope (improvement or rate of change), and error (residual) parameters. The Level 2 model estimates fixed (i.e. average), and random (i.e. individually varying) interindividual and intraindividual differences and can include predictors of individual/group differences in Level 1 parameters (i.e. intercept, slope). Detailed descriptions of these methods are available elsewhere (McArdle and Epstein, 1987; McArdle, 1988; McArdle and Hamagami, 1992; Snijders and Bosker, 1999; Verbeke and Molenberghs, 2000; Raudenbush and Bryk, 2002; Ferrer and McArdle, 2003; Singer and Willett, 2003). Conceptually, growth curve analysis involves estimating within-individual regressions of change or performance over time and on expected predictors of these individual regression parameters.

Multivariate multilevel models (MMLM)

One step towards higher complexity is to use more than one dependent variable. For the particular case of brain-behavior relationships, one automatically has multiple dependent variables of interest. In addition, within the domain of longitudinal structural brain data several levels of dependency need to be addressed in a statistical model. Measurements of GM or WM can be obtained for certain parcels nested within larger areas, nested within both hemispheres and obtained within individuals who were measured repeatedly over time. These data points are highly dependent on each other and any attempt to take this hierarchical structure into account will yield better parameter estimates in terms of biased and standard errors (e.g. Verbeke and Davidian, 2009). Multilevel or mixed-effects models are optimally suited to account for this dependency. Moreover, they make full use of the available data as they do not require that all participants have the same number of visits, or require all participants to be measured at common time points (cf., Raudenbush, 2001). To complicate matters, brain related data are also multivariate in the sense that GM or WM can be obtained from adjacent and correlated areas. To account for the multivariate nature of these data one may jointly examine the association structure in longitudinal change among different areas and composites within individuals. For example, Rast et al. (2017) modeled up to five dependent variables simultaneously over 8 years with a MMLM (MacCallum et al., 1997). In addition to estimating covariances among growth parameters (intercept and slope) the MMLM also accounts for covariances among all random effects between the different dependent variables. For example, in a model with random intercept and slope, the univariate MLM estimates the variance for both parameters (intercept variance and slope variance) as well as the covariance among the intercept and slope. In addition to these estimates, the multivariate MLM also accounts for the covariances among the dependent variables of the intercept and slope. That is, if five areas are included in the model as dependent variables, the MMLM estimates covariances for each of the random effect within and across these areas. In that case, the MMLM with random intercepts and slopes for each dependent variable estimates 45 different covariances and 10 variances. At the same time, the MMLM addresses seamlessly the issue of multiple comparisons, which typically arises in analysis of variance-type analyses. MMLMs do not necessitate pairwise comparisons and post-hoc alpha-value corrections because group mean comparisons are obtained via according coding patterns (e.g. dummy coding) that enter the model as predictors. With this approach, predictors compete for explained variance and significance tests of each predictor will be stringent. While the fit of the model to the data will increase with more parameters entering the model, the significance for each single parameter decreases. Further, multilevel techniques shrink group-level variances toward the mean, which inherently reduces the number of statistically significant comparisons, thus reducing the risk of type I errors in multiple comparisons (cf., Gelman et al., 2012). These classes of models can be expanded to address nonlinear trajectories or non-Gaussian processes. Moreover, they can be expanded to include submodels for the within-person variance structure. This is especially useful if within-person variability is the focus.

A note on the metric of change

In these models, a level and a slope parameter are generally specified for change relative to a particular time metric. The selection of the time metric is not trivial as it results in different models that reflect different assumptions about the underlying process of change. A common choice is to define the level as the initial point of measurement in a longitudinal data set whereas the slope parameter captures the rate of change over time in study. Especially in models with higher order terms or interactions (including all models with predictors of slope variance) the choice of the centering method influences the interpretation of the parameters (cf., Biesanz et al., 2004). The intercept or initial level should be carefully chosen to reflect the hypotheses tested in this context, especially when time-varying covariates are used as predictors of change (e.g. Curran and Bauer, 2011; Hamaker and Grasman, 2015; Wang and Maxwell, 2015).

While age heterogeneity of the sample is not a problem for growth models in particular, it is necessary to consider it in all cross-sectional or longitudinal models. Unlike traditional single-cohort longitudinal designs, individuals may vary considerably in age (and birth cohort membership) at each wave in the study, and the range of these between-person, cross-sectional, age differences tends to exceed the range of within-person, longitudinal, age changes over the course of data collection. A common technique to obtain ‘longitudinal’ data from studies with few (e.g. two) measurement occasions, is to combine the longitudinal with the cross-sectional age information by indexing change via the age of the study participants (e.g. Grimm et al., 2012). These age-heterogeneous samples were seen as an opportunity to virtually ‘accelerate’ longitudinal designs (e.g. McArdle and Bell, 2000; Mehta and West, 2000) by representing time as the different ages available in the study, rather than as time as the inception of the study. While this enables one to model growth trajectories that exceed the individual time-in-study span over the full age range they also bear the risk of confounding between-person differences with within-person change. That is, without the continued inclusion of baseline age differences, the resulting model produces estimates that represent a mix of the cross-sectional and longitudinal effects.

For models using chronological age as the time basis with a focus on random effects, it is important to keep in mind the variance component shrinkage due to the extrapolation beyond individual data (i.e. random effects will be estimated closer to the population mean) (e.g. Raudenbush and Bryk, 2002, Ch. 5). With greater age heterogeneity than study duration, the population mean will be dominated by the cross-sectional information. In addition, the confounding of between-person age differences and within-person age changes in longitudinal models muddles the potential for inference to increasingly selective, and thus conditional, ‘aging’ populations. Selectivity of participants must be accounted for as between-person sampling will be based on the proportion of the population who are alive (population mortality selection) and healthy but will also dropout from the study due to health and mortality causes. Such inference to aging populations must, therefore, be conditional on survival, and may be more directly obtained using between-person age differences and survival age (or time-to-death) as conditional predictors in a time-in-study longitudinal model (e.g. Johansson et al., 2004; Hoffmann, 2012).

Latent change models

Multilevel models can also be specified in the SEM framework, which has the advantage of incorporating additional models that operate at the latent level. For instance, instead of averaging dependent measures from several cognitive tasks into one composite score, a latent factor for the respective cognitive ability can be specified, thus estimating the shared variance among tasks while attenuating the effect of error variance. This also means that SEMs can be expanded to higher orders to include, for example, mechanisms of change. This can be in the form of latent growth models that define a linear (or nonlinear) model for lower order factors or in the form of LCS models that define the observed change from an occasion to the next as a sum of higher order factors. Moreover, SEMs easily lend themselves to measurement invariance (MI) testing. By constraining different elements of the measurement model, MI defines conditions under which meaningful comparisons among groups or within individuals across time can be drawn.

While most models discussed so far serve the field well, they might be considered static models because they define change resulting from static element such as the slope in a linear model. For example, Figure 5 represents a simple univariate latent growth model for five time points in the typical structural equation path diagram notation. The squares represent manifest variables (x1 to x5) and the circles represent latent, unobserved variables, the intercept (I) and the slope (S). Double-headed arrows denote undirected relationships such as covariances and single-headed arrows represent directed relationships such as regression weights, or loadings. Both, the intercept and slope have associated variances that capture the individual differences therein. Moreover, the intercept and slope are allowed to covary.

Figure 5:

A univariate latent growth curve model. Circles represent latent variables while squares represent manifest variables.

One headed arrows denote directed relationships and double headed arrows represent undirected relationships. Here, I is the latent intercept and S is the latent slope, each with their corresponding variances σI2 and σS2.

Another approach is to capture the change trajectory through models that originate in dynamical systems where the current state of the system is defined by previous states of the system (e.g. Boker and Wenger, 2007). Notably, the LCS (McArdle and Hamagami, 2001; McArdle, 2009) model and its multivariate extension, the bivariate LCS have been applied successfully in recent years to longitudinal data. The LCS addresses change, from one time point to the next, from a SEM standpoint. That is, while one could index change from one time point t–1 to t on the observed data, the LCS indexes these changes at the latent level, thus separating measurement error from the true score. Once the differences among time points are defined, the LCS focuses on the rate of change, rather than latent change itself. Figure 6 represents a basic LCS for one common factor over five time points. The manifest variables (x1 to x5) are again symbolized by squares. η1–η5 represent latent true scores, Δη0–Δη4 are the LCS and I and S define the latent intercept and slope, or rate of change. Unlabeled paths are fixed to 1. Here, the first change score is defined as Δη0. The change does not affect the prior score η1 but it does influence the second true score directly and it is an indirect part of all the other latent variables. The same holds for the following change scores. α paths represent constant change and β paths represent proportional change from the variable measured at the previous time point. The rate of change is passed into the latent change scores, typically with a constant weight of 1 for equally spaced time intervals. Essentially, the rate of change is defined as the difference between two latent variables divided by the length of the given discrete time interval among them. A constant rate of change would be nothing else than the first partial derivative of a linear function with respect to time–but with nonlinear changes, the rate of change will take different values for different measurement occasions.

Figure 6:

A univariate latent change score model. x1–x5 represent the observed variable measured at five time points, η1–η5 represent latent true scores, Δη0–Δη4 are the latent change scores and I and S define the latent intercept and slope α paths represent constant change and β paths represent proportional change from the variable measured at the previous time point.

While the constraint for discrete time seems rather restrictive, Voelkle et al. (2012) expanded the LCS to a continuous time model where this constraint is resolved. Importantly, LCS and continuous time models (and variants thereof) can be readily expanded to the multivariate case which makes them ideal candidates for modeling correlated changes in brain related and cognitive longitudinal data. Moreover, given that these models do not impose a functional form of change, they are very flexible and can handle a multitude of curvilinear trajectories in one or more processes and relate changes in one variable to changes in another. While the adoption of latent change models is slow, likely due to a rather high level technical sophistication in order to implement these models, new software developments now facilitate the use of LCS models (see Kievit et al., 2018 for a tutorial). For example, to depict the models in Figures 5 and 6, we used Ωnyx (von Oertzen et al., 2015), a freely and openly accessible graphical tool that provides an easy and intuitive approach to depicting SEM-based models.

Advanced models

Besides the models discussed above, other methodological advances have recently emerged and/or are being developed that are of particular relevance for aging and lifespan studies. For example, growth mixture models permit the identification of subpopulations that exhibit distinct multivariate patterns of change and are therefore well suited for exploratory analyses. Similar to latent class models, growth mixture models (e.g. Muthén, 2001) assume that the sample is composed of members from more than one population that exhibit distinct patterns of change. Using individual response patterns in a longitudinal setting with repeated measurements to define trajectories, growth mixture models (1) identify homogeneous groups of individuals or trajectory classes, (2) assign each participant a probability of belonging to a particular trajectory class, and (3) use class membership information to estimate the influence of individual characteristics on trajectory shape. A related, but less familiar method are SEM trees (Brandmaier and McArdle, 2013), which split the data into homogeneous subgroups based on a set of predictors and fit an SEM separately to each of these subgroups (see Jacobucci et al., 2017, for a comparison of the two methods). In contrast with other SEM-based statistical approaches, SEM trees are designed as an exploratory method. Especially in light of the many variables that influence aging, such approaches of data reduction gain more and more importance.

Ultimately, most of the above-discussed models can also be estimated in a Bayesian framework. The Bayesian approach to inferential statistics has the advantage that it can overcome the typical problems surrounding the p-value in null hypothesis testing (e.g. corrections for multiple comparisons), and allows to incorporate previous knowledge about the expected effect into the analysis (Kruschke, 2010). For example, Bayes Factors provide an estimate of the strength of evidence both for the null hypothesis (i.e. absence of the effect), and the alternative hypothesis (i.e. presence of the effect), necessitating researchers to think about what they would actually consider plausible values for the alternative hypothesis (Dienes, 2014). Thus, using Bayesian estimation, it is possible to test specific theoretical predictions, and gain an estimate of the strength of the evidence for the presence or absence of the predicted effect. Recent software developments have provided novel tools to efficiently estimate Bayesian models of change both in the MLM (Bürkner, 2017) and the SEM framework (Asparouhov and Muthén, 2010; Merkle and Rosseel, 2016).

Overall, a wide range of longitudinal modeling tools now exist or are emerging that can capture multivariate change and correlated change with models that are able to accommodate a wide range of developmental questions in brain and cognitive aging.