Insulin Use in Type 2 Diabetes and the Risk of Dementia: A Comparative Population-Based Cohort Study

The association between type 2 diabetes and dementia has been examined extensively, with a general consensus linking the two conditions (1,2); however, the literature on the possible association between the use of different classes of antihyperglycemic agents and the incidence of dementia is inconclusive (3). Several classes of antihyperglycemic medications, including metformin, thiazolidinediones, and, more recently, the sodium–glucose cotransporter 2 (SGLT2) inhibitors, have been linked to a lower risk of incident dementia by observational studies, with supporting findings from pharmacology research proposing insulin-sensitizing, anti-inflammatory, and various cardiovascular and cerebrovascular mechanisms (3–6). Conversely, insulin use has been associated with an increased risk of dementia in several observational studies (3,4), albeit the pharmacological impact of insulin on the pathophysiology of dementia is not fully understood, and mechanisms with conflicting directions have been hypothesized (7).

Results from landmark interventional trials do not show an association between insulin and cognitive decline. In a substudy of the Outcome Reduction With Initial Glargine Intervention (ORIGIN) trial, the rate of change of cognitive test scores and the incidence of probable cognitive impairment did not differ between the insulin glargine and standard care groups after a median follow-up of 6 years (8). Similarly, results from the Action to Control Cardiovascular Risk in Diabetes - The Memory in Diabetes (ACCORD-MIND) trial showed that insulin use was not associated with changes in cognitive performance over 40 months (9). Thus far, no interventional studies have assessed the incidence of dementia as an outcome, because of the long follow-up period required and difficulty in retaining the study population. Therefore, most evidence on the association of antihyperglycemic medications, including insulin, with the risk of dementia stems from observational studies. Specifically, results from a 2019 systematic review and meta-analysis of six cohort studies suggested that insulin was associated with a 21% increased risk of dementia (3). Similarly, a pooled analysis of five cohort studies suggested that insulin use is associated with a 58% increased risk of new-onset dementia (4).

Despite the development in recent years of methods used in observational drug effect studies, much of which has focused on causal inference, many challenges remain. Confounding by indication has been arguably the biggest challenge facing observational studies assessing the safety and effectiveness of medications in routine clinical care (10). Indeed, multiple studies assessed the use of insulin compared with not having diabetes (11–13), thereby introducing imbalance on several confounding factors, including diabetes itself and all of the cardiovascular and cerebrovascular complications that accompany it. More granularly, type 2 diabetes is a chronic condition, with several pharmacological options used at different disease stages throughout the life course of a patient with diabetes; hence, concerns of confounding by severity of diabetes also require mitigation through design (14,15). This issue is heightened with insulin, as it is often used for more severe diabetes in routine clinical care. Indeed, confounding by disease severity has been shown to play a role in other pharmacoepidemiologic studies evaluating insulin and cardiovascular or cancer outcomes (16,17). While the new user active comparator design has been adopted as a gold standard design to assess the effect of diabetes medications, the implementation of this design is more complex because of the lack of an obvious active comparator for insulin (10,15).

We hypothesized that at least some of the previously reported positive association between insulin and dementia is explained by confounding by severity of indication. Herein we re-examine the association between insulin use and the risk of dementia while addressing this threat to validity through design and analysis.

This was a retrospective population-based cohort study using administrative health care data from British Columbia (BC), Canada (1 January 1996 to 31 December 2018). In BC, health care is provided through a publicly funded compulsory program through the provincial government to almost all BC residents except members of the armed forces, Royal Canadian Mounted Police, and federal penitentiary inmates. For administrative purposes, data on all hospital admissions, physician visits, prescription medication claims, births, deaths, and health care plan registration and cancellation are captured and housed at Population Data BC (https://www.popdata.bc.ca/data) (18–22). Therefore, the data source is comprehensive and representative of BC residents regardless of age, sex, ethnicity, or socioeconomic status (SES).

Data were linked across six databases using a deidentified personal health identification number. These databases included 1) the population registry (Consolidation File), which provided the date of birth, sex, and dates of health care coverage (18); 2) the Medical Services Plan, which provided data on physician visits, including the service date and the International Classification of Diseases, 9th Revision (Clinical Modification) (ICD-9-CM) diagnosis code (19); 3) the Discharge Abstract Database, which provided hospital admission and discharge dates and several diagnoses coded using the ICD-10-Canadian Adaptation codes (20); 4) the PharmaNet program, which includes the drug dispensing date, name, drug identification number, and days supply (21)—importantly, all nonhospital prescription drugs dispensed by community pharmacies to BC residents, regardless of the type of insurance coverage (government-sponsored, private, or out-of-pocket), are captured; 5) the Vital Events Deaths database, which provided the date of death (22); and 6) Census Geodata, from which we acquired an area-level measure of SES based on the first three characters of the postal code and aggregated neighborhood-level income data (23).

First, we created a cohort of patients with incident diabetes who were diagnosed between 1 January 1998 and 31 December 2016. Patients were required to have continuous registration in the population registry for at least 2 years prior to diabetes onset. We used this 2-year period as a washout period, during which patients did not receive any diabetes diagnosis codes or any antihyperglycemic medications to ensure diabetes was incident. Diabetes was defined based on the validated case-defining algorithm from the Canadian Chronic Disease Surveillance System, whereby diabetes is defined as the earliest occurrence of two physician claims or one hospitalization captured by relevant ICD codes within a 2-year period (24). This definition has an 81.9% positive predictive value and 98.7% negative predictive value (24,25). To minimize capturing type 1 diabetes cases, those who received insulin monotherapy as first-line treatment were excluded.

Our exposure contrast of interest was new insulin use compared with new non-insulin use. To minimize confounding by severity of indication, multiple design approaches were used. As there is no single clinically appropriate active comparator to insulin that is used at a similar disease stage, we created a subcohort of those who received two distinct noninsulin antihyperglycemic classes. From this subcohort, we identified new users of insulin compared with new users of a noninsulin class. The purpose of this approach was to provide more balanced exposure groups with regards to the diabetes disease stage, wherein both insulin and the comparator are used as third-line therapies. We used a new user design, and the index date was either the date of insulin initiation (i.e., first prescription as a third line) for those exposed or the date of initiating a third antihyperglycemic class for those unexposed.

Then the analytical cohort was restricted to those who met the following criteria: 1) aged between 40 and 70 years at index date, with the lower limit set to allow enough follow-up time to capture incident dementia, while the upper limit was set to minimize the possibility of including patients with an early stage of dementia not yet recognized, diagnosed, or captured with administrative data; 2) no previous record of diagnostic codes indicating dementia or a medication claim record for a cholinesterase inhibitor or memantine before index date; 3) no diagnosis of Down syndrome, given the high risk of diabetes and dementia in Down syndrome with genetic variation that we were unable to assess; and 4) a latest index date of 31 December 2016 to ensure a minimum follow-up of 2 years.

Incident all-cause dementia was defined using a validated algorithm that requires one hospitalization code, three physician claims codes (at least 30 days apart in a 2-year period), or a prescription filled for a cholinesterase inhibitor (26). This definition has been validated using Canadian data with 80.4% positive predictive value and 99.0% negative predictive value (26). The outcome was restricted to all-cause dementia and did not explore subtypes of dementia, given the difficulty in ascertaining these subtypes using administrative data and the possibility of mixed dementia (26). Similar to previous pharmacoepidemiological studies, a lag period was used to account for existing dementia that was not yet diagnosed and to also allow for the disease process to occur (27–29). Therefore, those who received a dementia diagnosis within 2 years of index date were censored (27–29).

We used two analytic approaches to minimize confounding. First, we adjusted for important potential confounders including age, biological sex, and SES, as well as proxies of diabetes severity such as diabetes duration, the presence of microvascular and macrovascular complications, and any previous hypoglycemic episodes. We also included other conditions, such as depression, and the use of other medications, including statins, antacids, and antihypertensives. These covariates were assessed within 365 days before index date. A full list of all included potential confounders is reported in Supplementary Table 1.

Second, we further improved covariate balance using inverse probability of treatment weighting based on high-dimensional propensity scores (hdps), which have been found to improve adjustment for confounding (30,31). Specially, we augmented the aforementioned predefined variables with 500 additional variables that were empirically identified and prioritized through an automated technique that examines thousands of potential covariates from five dimensions (hospitalizations, procedures, medical diagnoses, medical services, and prescription medication claims). The empirical variables were also assessed within 365 days before index date. We then used multivariable logistic regression to model the probability of exposure to insulin, based on the predefined and empirical covariates. The estimated propensity scores were then used to compute the inverse probability of treatment weights (IPTW), which were stabilized to reduce the variance associated with any extreme weights (31,32). We assessed balance of baseline covariates after weighting using absolute standardized differences (ASD), with ASD > 0.10 considered as significant imbalance (33).

Patients were followed from index date until dementia diagnosis or 31 December 2018. We censored at the first occurrence of either emigration, end of registration, death, or switching from exposure groups. Specifically, for insulin users, we censored when patients discontinued insulin (>180-day gap), and, for noninsulin users, we censored when patients received insulin. The hazard ratio (HR, 95% CI) of dementia was estimated using cause-specific hazards models with death as a competing risk.

A list of all ICD codes used to capture medical conditions, including diabetes, dementia, and covariates, is reported in Supplementary Table 2.

In a series of secondary analyses, we assessed possible effect modification of the association between insulin use and dementia by age (as a continuous variable), biological sex (female versus male), SES (quintiles), and the number of distinct classes of medications (0–3, 4–7, 8–11, ≥12 classes) as a proxy measure for overall comorbidity status at baseline (34).

Specifically, in five additional weighted models, an interaction term was included in addition to the main effect terms. In the model in which SES was assessed, those with unknown income quintile (roughly 2–3%) were excluded from the analysis. For each model, we tested the statistical significance (P value < 0.05) of the interaction term using the Wald test. If the interaction term was a significant predictor, we calculated the HR of dementia for each level of the potential effect modifier using a linear combination of parameters.

We conducted three sensitivity analyses. First, since sulfonylurea is also a class of diabetes medications that has been reported to increase the risk of dementia, we conducted a sensitivity analysis wherein we excluded those who initiated sulfonylurea as a third class in the noninsulin comparator group or those who were on sulfonylurea at the time of the third-class initiation. Moreover, we censored those who received sulfonylureas after index date in both exposure groups. Sulfonylurea use before index date was adjusted for in the model. Second, we repeated all primary analyses using new insulin compared with new noninsulin use, but as a fourth rather than a third therapy. Third, we changed the grace period used to define the exposure end from a gap of 180 days to 90 days or to a gap of any length.

All analyses were conducted using SAS version 9.4 (SAS Institute Inc., Cary, NC).

This study was not registered in a trials database. The study protocol including details relating to the design and analyses was completed before conducting the study and was reviewed and approved by the data providers. The study protocol is not publicly available.

All data were deidentified, and no personal information was available at any point of the study. Access to data provided by the Data Steward(s) is subject to approval but can be requested for research projects through the Data Steward(s) or their designated service providers. All inferences, opinions, and conclusions drawn in this publication are those of the author(s) and do not reflect the opinions or policies of the Data Steward(s). Ethics approval was also obtained from the University of Waterloo, Waterloo, Ontario, Canada.

We included 414,089 patients with newly diagnosed type 2 diabetes. Our final analytical cohort included 7,863 new users of insulin as a third-line class and 25,230 new users of a noninsulin third-line class (Fig. 1). Before ITPW, the mean (SD) age was 57.3 (7.8) years for insulin users and 57.0 (7.7) years for noninsulin users, while the mean duration of diabetes was 6.1 years for insulin users and 6.3 years for noninsulin users at index date (Table 1). Patients using insulin were more likely to have multiple hospitalizations and physician visits and be on more distinct classes of medications, indicating higher use of the health care system. The frequency of several microvascular and macrovascular complications, including ischemic heart disease, nephropathy, and peripheral vascular disease, in addition to other morbidities such as anxiety, was also higher among insulin users (Table 1). IPTW resulted in well-balanced groups across all the included potential confounders, wherein high ASD for most characteristics were reduced to levels of little concern (<0.10) (Table 1).

A total of 78 all-cause dementia events occurred over a median (interquartile range) follow-up period of 3.9 (5.9) years among insulin users and 179 events over 4.6 (4.4) years among noninsulin users (Table 2). A Kaplan-Meier curve stratified by exposure status is reported in Supplementary Figure 1. The crude incidence rate (95% CI) of dementia was 2.13 (1.71–2.66) per 1,000 person-years for insulin users and 1.31 (1.13–1.51) per 1,000 person-years for noninsulin users (Table 2). The weighted incidence rates were 1.61 (1.24–2.09) per 1,000 person-years for insulin users and 1.43 (1.24–1.65) per 1,000 person-years for noninsulin users (Table 2).

Before any mitigation of confounding by analysis, the crude HR (95% CI) for all cause-dementia for insulin versus noninsulin use was 1.68 (1.29–2.20). After adjusting for baseline confounders using a multivariable regression model, the estimate was attenuated (HR = 1.39; 95% CI = 1.05–1.86). Further adjustment through hdps weighting led to even more attenuation of estimates, with the association no longer reaching statistical significance (HR = 1.14; 95% CI = 0.81–1.60) (Table 2). These overall findings were consistent across all sensitivity analyses (Fig. 2).

Results from the secondary analyses did not indicate potential effect modification of the association between insulin and dementia (P value for the interaction term) by age (P = 0.50), sex (P = 0.50), SES (P = 0.30), or the number of distinct medications at baseline (P = 0.67).

Findings from this comparative cohort study did not show that insulin use is associated with an increased risk of dementia. These results are in line with our hypothesis that at least some of the previously reported association between insulin use and dementia is likely explained by confounding by severity of diabetes. Indeed, results from our study negate findings assessing this association in most previous cohort studies that are weakened by methodological limitations in the design (11–13,35–39). Specifically, in observational studies wherein insulin use was compared with not having diabetes, the risk estimates ranged from 1.40 to 4.30 (11–13). Restricting the cohort to diabetes patients in some studies attenuated the risk estimate, albeit still indicating an increased risk (35–39). However, our results are in line with a more recent nested case-control study showing insulin is not associated with an increased risk of dementia (OR 0.93; 95% CI 0.83–0.99) (40). Despite using data from the well-established Danish registry, the study by Wium-Andersen et al. (40) was not specifically designed to assess insulin but rather all antidiabetic classes and used other methods to adjust for confounding.

Our study highlights that when studying the effects of medications for chronic diseases wherein there is escalation of medication classes throughout the life course of the disease, such as in the case of type 2 diabetes (14), design approaches and the careful consideration of the comparator group are critical (15). While insulin does not have a clear active comparator, aligning the comparator group based on an indicator of diabetes severity is a possible approach. In this study, we used the therapeutic history to manage diabetes as an indicator of diabetes severity and the failure to control for hyperglycemia. This also allowed for a distinct index date and therefore the covariate assessment period to cover a similar disease stage. While matching the cohort based on diabetes duration is also an option, diabetes duration may not be an optimal marker of diabetes severity. For example, an individual could have well-controlled diabetes while on metformin only for a duration of 5 years compared with someone who also had diabetes for 5 years but who had been on several medications. In fact, this is evident in our study: through design, some balance between groups on various indicators of diabetes severity, including diabetes duration, retinopathy, and neuropathy, was achieved before weighting.

Nevertheless, adjusting for confounding through design only is not sufficient, and a further adjustment through analysis is necessary. Results from this study show that, using a conventional multivariable adjusted model, estimates were attenuated compared with the crude model, albeit still indicating a significantly higher risk of dementia. This was despite including a wide range of potential predefined confounders based on clinical knowledge. Notably, results were no longer statistically significant after further adjustment through the use of the inverse probability of treatment weighting approach based on hdps which, included 500 more empirical variables.

This study shows an example of the complementary role of design and analysis to combat confounding by severity of indication in observational studies of chronic disease medications, highlighting the need for robust methodology to better answer important clinical questions pertaining to dementia risk. This is particularly true given that randomized controlled trials (RCTs) are not feasible to assess the safety of insulin on a long-term outcome such as dementia, rendering observational studies as the main source of evidence to inform practice.

Clinically, these results provide insight to health care providers and diabetes patients by providing robust epidemiological evidence on the association between insulin and the risk of dementia. In contrast to most other previous studies, findings from this investigation suggest insulin use may not be associated with dementia. As most patients with uncontrolled type diabetes 2 eventually start insulin therapy, this may reduce anxiety about insulin use. Nonetheless, it is important to note that the upper limit of the CI in our analysis (1.60) does not rule out a potential increase in dementia risk associated with insulin use that was suggested by previous meta-analyses (3,4). Future work should further detail the relationship between the different types and regimens of insulin as well as insulin dosing.

Additionally, our findings provide real-world evidence that can help direct future studies on the role of insulin in cognition in light of the contradictory evidence around the pharmacological hypotheses relating insulin to dementia (7). On the one hand, insulin is hypothesized to improve cognitive function because of its neuromodulatory actions in the brain, including synaptic formation and remodeling, regulation of neurotransmitters, and amyloid clearance (7). Indeed, several trials have been conducted to assess the efficacy of intranasal insulin in improving cognition, albeit without yielding any promising results (41). On the other hand, hyperinsulinemia is thought to be linked to Alzheimer’s dementia because of the downregulation of the insulin degrading enzyme, for which both insulin and amyloid β are competing substrates (7).

This study has several strengths, including the implementation of a new-user design, mitigation of confounding through a novel design approach and established analysis techniques, and the use of a comprehensive data source for all BC residents with a high level of insurance coverage and a span of over 20 years. Additionally, several secondary analyses to test for effect modification and sensitivity analyses to ensure consistency in results were conducted.

Despite the strengths of this study, there are some limitations. First, although the weighted HR did not reach statistical significance, the upper limit does not rule out the possibility of a higher risk of dementia with insulin use. In addition to the conservative number of dementia outcomes, the median follow-up time was short, roughly 4 years. A reanalysis in a larger population or from multicenter cohorts with longer follow-up would be helpful to confirm our overall finding. Second, given the use of administrative data, there is a potential for misclassification of type 2 diabetes and dementia, despite using validated algorithms to define both conditions. Specifically, measures of glycemia and cognitive function for each individual were not available. Third, drug exposure was based on outpatient prescription claims, and, therefore, the actual consumption of medications can only be assumed. Fourth, we only assessed all-cause dementia as an outcome, as it is difficult to accurately differentiate between subtypes. Fifth, data on ethnicity; lifestyle indicators, such as BMI; education; laboratory measures, such as HbA_1c and creatinine; and genetic determinants of dementia, including apolipoprotein E, were not available; therefore, residual and unmeasured confounding remains possible. Importantly, response to insulin seems to differ based on the presence of the apolipoprotein E gene, indicating potential effect modification that we are unable to explore (41). Last, we assessed third-line exposure to insulin, which may impact the generalizability of results; however, in a sensitivity analysis, we also defined exposure as fourth line.

Findings from this population-based cohort study did not show that insulin is associated with an increased risk of all-cause dementia. These findings highlight the importance of adjusting for confounding through design and analysis techniques in observational studies. Clinically, this overall conclusion negates the conclusions of previous studies and provides further insight to inform clinician-patient discussions about diabetes management.

Acknowledgments. This work was performed in partial fulfillment of the requirements for a PhD degree for W.A.

Funding. This project is funded by the Mike & Valeria Rosenbloom Foundation Research Award at the Alzheimer’s Society of Canada.

Duality of Interest. No potential conflicts of interest relevant to this article were reported.

Author Contributions. W.A. conceived the study idea, designed the study, conducted all analyses, and wrote the first draft of the manuscript. J.-M.G. supervised the work. All authors contributed to the study conception, design, and analysis protocol. All authors approved the final version of the article. W.A. and J.-M.G. are the guarantors of this work and, as such, had full access to all the data in the study and take responsibility for the integrity of the data and the accuracy of the data analysis.