In a large cohort study of an elderly population-based sample, we observed no reduction in risk of dementia or AD among users of NSAIDs. Instead, we found that prior sustained NSAID exposure was associated with increased incidence of dementia and AD. This result was robust to comprehensive sensitivity analyses investigating features of both the design and analytic approach.
Interest in NSAIDs for AD treatment or prevention began in 1990, when patients with rheumatoid arthritis (for the most part, obligatory users of NSAIDs) were reported to show reduced rates of Alzheimer pathology.19
Several early studies20,21
then spurred speculation that anti-inflammatory treatments including NSAIDs could delay or prevent the onset of AD. Subsequently, numerous observational studies reported data consistent with this notion. Notably, a population-based prospective study from Rotterdam examined individuals aged 55 years and older who had NSAID prescription information from a computerized pharmacy dispensing database.6
A 2004 meta-analysis of three carefully conducted case-control studies and four cohort studies showed convergent odds ratios (ORs) or hazard ratios (HRs) near 0.6, suggesting a 40% lower incidence of AD among those exposed.22
A more recent meta-analysis of six population-based prospective studies suggested an HR of 0.75 (95% CI, 0.64–0.89),2
but no difference in apparent effects of categories of NSAIDs that were distinguished by their ability to reduce production of the amyloidogenic peptide Aβ42 in vitro. A large recent case-control study using the national VA database found an OR of 0.76 (95% CI, 0.68–0.85) with 5 years of NSAID use.23
However, the AD–NSAIDs relationship may be more complicated. NSAIDs are not helpful for people with established AD,4
and rofecoxib does not allay progression of milder cognitive symptoms to AD.5
NSAIDs also appear to offer no benefit to people whose preclinical AD pathology is sufficiently advanced to produce dementia symptoms within very few years.6,7
ADAPT, which followed participants for only 24 months on average after randomization, yielded relative risks of 1.99 (95% CI, 0.80–4.97) and 2.35 (95% CI, 0.95–5.77) in those assigned to celecoxib or naproxen vs placebo.
Similarly, the present findings appear to contradict the straightforward hypothesis of reduced incidence with NSAID exposure, and they contrast with results from many prior studies, including the methodologically similar Rotterdam study.6
Why? Possibly owing to several methodologic strengths, we may have observed a truer representation of the association of NSAIDs and dementia risk than others before us. These strengths include not only a community-based sample but also biennial assessment for dementia and AD, rigorous exposure classification based on pharmacy dispensing records beginning in 1977 (17 or more years before initial enrollment into ACT), large numbers of incident dementia or AD cases affording good statistical power, and consideration to self-reported as well as pharmacy-based exposure data. Some confidence in the robustness of our observations is also suggested by the consistency of the associations observed in a variety of models using several methods of exposure classification and multiple outcomes, including several sensitivity analyses. On balance, these strengths appear to outweigh the weaknesses in our study, which include a sample which, although representative of its population base, might not generalize well to other populations, lack of precise dosing information, and (inherent in all observational studies) the possibility of bias from inadequately measured or unsuspected confounders.
Upon reflection, however, we pursued other explanations for the discrepancy. For example, unlike the Rotterdam investigators, we had detailed information on NSAID exposure for many years before enrollment. This might arguably have reduced misclassification of individuals as nonusers who had heavy NSAID exposure before enrollment. However, sensitivity analyses ignoring earlier exposures did not change our results (e-appendix). Alternatively, NSAID use might have promoted AD onset in a particular group of susceptible individuals with unrecognized advanced preclinical AD pathology, as appeared likely in ADAPT.8
Arguably, these nondemented individuals had advanced AD pathology because they developed dementia within such a short time and, given its advanced age, the ACT cohort may have included many such individuals. Again, however, this explanation was not supported by a sensitivity analysis of distant vs recent exposures, which found no reduction in dementia or AD risk in participants with distant heavy exposures only (e-appendix).
We therefore considered whether the most likely explanation of the discrepant findings related to differences in participant ages across studies. The ACT cohort is older than most previously studied populations, with a minimum enrollment age of 65 years and a median age of 83.5 years (interquartile range, 79.6–86.9) at dementia onset. By contrast, the Rotterdam cohort was much younger, with 45% of participants younger than 65 years at enrollment. The Cache County Study7
cohort was also younger, with a mean age of 74 years at dementia assessment. The latter figure is broadly typical for most prior studies, which have formed the evidence base for reduced incidence of AD in NSAID users.2
The Cache County Study also found an interaction between age and AD incidence in NSAID users, such that an aHR of 0.38 at the mean age of 74 was increased by 7% with each year of age. We regarded this sort of modification of effect by age as potentially important because, similar to present results, two other studies of substantially older cohorts, the Religious Orders Study3
and the MoVIES project (median dementia onset near age 80),24
failed to show a reduced risk of AD, with aHRs of 1.19 (95% CI, 0.87–1.62) and 1.16 (95% CI, 0.82–1.63; data from reference 7). Upon closer inspection, however, this level of interaction appeared too modest to explain our unexpected results, and probably those of the Religious Orders Study or MoVIES as well.
How else might differences in cohort age account for different results? Others have suggested that differences across age groups may be attributable to selection bias.25
We attempted to control for such cohort effects by stratifying our analyses by 5-year age groups at enrollment. However, this technique produced little change in results (data not shown). We also considered one other explanation that, if substantiated, might simultaneously explain our results and also account for opposite findings from younger cohorts. A part of our hypothesis was that NSAID exposure delays the onset of AD. Indeed, it is commonly conjectured that most, if not all, AD risk factors act by accelerating or retarding dementia onset. This phenomenon has been shown repeatedly for APOE
and it appears also to apply to head injury.28
In fact, we know of no AD risk-modifying factor that demonstrably acts otherwise. If NSAID exposure defers the onset of AD, then exposed members of younger cohorts would logically show a reduced frequency of disease, but NSAID users in older cohorts could be enriched for cases that would otherwise have appeared earlier.