Study of Azeliragon in Patients With Mild Alzheimer's Disease and Impaired Glucose Tolerance: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Azeliragon in Patients With Mild Alzheimer's Disease and Impaired Glucose Tolerance (NCT03980730), a randomized phase 2 study. The primary outcome is Part 1 : Change From Baseline in the Alzheimer's Disease Assessment Scale - Cognitive Subscale (ADAS-cog14) at Month 6.

2. Clinical Question

3. Trial Design

The registry describes a Phase 2 randomized, double-blind, placebo-controlled, multicenter study. Its design is parallel-group, with quadruple masking recorded. The study evaluated azeliragon and placebo in patients with mild Alzheimer’s disease and impaired glucose tolerance. Randomization allocated participants to the two treatment groups; the posted Part 1 outcome counts were 21 for azeliragon and 22 for placebo.

In Part 1, azeliragon was a 5mg capsule taken orally once daily for 6 months, and the placebo was a matching capsule taken on the same schedule. The registry’s brief description gives approximate participation durations of 9 months in Part 1 and 21 months in Part 2. The primary outcome was assessed from baseline to Month 6, so the result concerns the shorter Part 1 assessment rather than a longer-term comparison.

The registry lists enrollment of 43, a start date of 2019-06-27, a primary completion date of 2020-12-01, and a status of terminated. The reason for termination is not reported in the registry record. The registry record also does not report the trial’s original sample-size justification or the design assumptions used to choose its enrollment target. The displayed planning illustrations are based on the observed results and should not be read as the trial’s original design plan.

The full analysis set is described as including randomized participants who had at least one post-baseline assessment, regardless of whether they received study medication. The registry states that this set was used for all efficacy hypothesis tests. It does not report further details about the handling of missing assessments or the statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) includes all randomized subjects, whether or not they receive any study medication, and who have at least one post-Baseline assessment. The FAS was used for all hypothesis tests of efficacy.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Part 1 : Change From Baseline in the Alzheimer's Disease Assessment Scale - Cognitive Subscale (ADAS-cog14) at Month 6, measured over Baseline to Month 6.

The primary endpoint was change from baseline to Month 6 in the Alzheimer’s Disease Assessment Scale–Cognitive Subscale 14 Item, or ADAS-cog14. The scale ranges from 0 to 90, with higher scores indicating greater cognitive impairment. A change score describes how a participant’s measured score differs at follow-up from their baseline score; the group summary therefore concerns average change over the assessment period, rather than the Month 6 score alone.

Cognitive scales are used in trials of Alzheimer’s disease to quantify performance in a consistent way and to make comparisons between treatment groups. ADAS-cog14 is the primary measure named in this study’s Part 1 outcome. Its direction matters for interpretation: a higher score represents greater impairment, so a positive change is movement toward a higher score on the scale. The registry does not provide a threshold for interpreting the size of an individual change as clinically important.

The posted group estimates are least-squares means: 1.8 for azeliragon and 0.4 for placebo. Least-squares means are model-based group estimates rather than simply a description of every participant’s individual trajectory. The registry’s sponsor-reported analysis used mixed models, but its model estimate and confidence interval are not reported in the registry record. The posted summary estimates and the sponsor’s reported hypothesis test therefore provide different pieces of information: the estimates describe the observed group summaries, while the reported p-value gives the result of the sponsor’s stated analysis.

7. Results Posted in the Registry

• Azeliragon: mean 1.80 versus 0.40 on control; difference 1.40 (95% CI -0.70 to 3.50), standardized effect d = 0.40; z-test p = 0.191.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Part 1: Change From Baseline in the Amsterdam-Instrumental Activities of Daily Living (Amsterdam-IADL) at Month 6

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Azeliragon: mean 6.20 versus 9.30 on control; difference -3.10 (95% CI -9.17 to 2.97), standardized effect d = -0.30; z-test p = 0.316.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Azeliragon and the control. The interval gives the range of effects that remain compatible with the data.

Part 1: Change From Baseline in the Clinical Dementia Rating Scale-Sum of Boxes (CDR-sb) at Month 6

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Azeliragon: mean 0.60 versus 1.30 on control; difference -0.70 (95% CI -1.61 to 0.21), standardized effect d = -0.46; z-test p = 0.130.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Azeliragon and the control. The interval gives the range of effects that remain compatible with the data.

Part 1: Change From Baseline in the Functional Activities Questionnaire (FAQ) at Month 6

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Azeliragon: mean -0.50 versus 2.80 on control; difference -3.30 (95% CI -5.63 to -0.97), standardized effect d = -0.85; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Azeliragon than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes show a varied pattern rather than a consistent signal across all measures. The Amsterdam-IADL and CDR-sb recalculated intervals include zero, whereas the Functional Activities Questionnaire interval is below zero and its unadjusted p-value is 0.005. Numerical results for the MMSE outcome are not reported in the registry record. This overview describes the pattern without treating any one secondary result as confirmation of the primary finding.

The primary endpoint was ADAS-cog14 change, and its recalculated interval includes zero; the sponsor’s mixed-model p-value was 0.206. Secondary measures assess related but distinct aspects of function and cognition, so their results can add context but do not replace the primary endpoint. The registry does not report an adjustment for multiple comparisons or a testing hierarchy. Where several outcomes are examined, an unadjusted result is more vulnerable to chance findings across the set of tests and should be interpreted cautiously.

The functional activities result may appear more pronounced than the other posted secondary recalculations, but one unadjusted result among several outcomes is not, by itself, strong evidence of a reliable treatment effect. Its interpretation depends on the analysis plan, missing-data handling, and multiplicity strategy, which are not reported in the registry record. Nor does the available record establish whether the secondary outcomes were intended as confirmatory or exploratory.

Overall, the secondary results add descriptive information but do not resolve the uncertainty around the primary comparison. Their mixed pattern, the missing numerical MMSE result, and the lack of a reported multiplicity approach all limit how much weight can be placed on apparent differences among individual endpoints.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Part 1: Change From Baseline in the Amsterdam-Instrumental Activities of Daily Living (Amsterdam-IADL) at Month 6
• Part 1: Change From Baseline in the Clinical Dementia Rating Scale-Sum of Boxes (CDR-sb) at Month 6
• Part 1: Change From Baseline in the Functional Activities Questionnaire (FAQ) at Month 6
• Mean Change From Baseline in the Mini Mental State Exam (MMSE) at Month 6.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a numeric score, and the registry reports group mean changes. The primary arm values are least-squares means, with standard errors of 0.82 for azeliragon and 0.69 for placebo. A standard error describes the uncertainty in an estimated mean; it is not the spread of individual participants’ scores. The outcome counts were 21 and 22, respectively. The registry does not give the sponsor model’s estimated treatment contrast or its confidence interval.

What does the sponsor’s mixed-model test address?

The registry reports a Mixed Models Analysis for superiority, with p = 0.206. In general, a mixed model can represent repeated observations from the same participant and account for their correlation, while estimating group patterns over time. That general description does not establish which exact model terms, covariance structure, or missing-data assumptions were used in this study. Those details are not reported in the registry record. The reported p-value is the sponsor’s test result; without the model estimate and confidence interval, the direction and precision of that model-based contrast cannot be read from the p-value alone.

What is the unadjusted recalculation?

The recalculated primary mean difference is 1.4, formed from the posted group summaries. Its confidence interval is -0.701 to 3.5, and the unadjusted p-value is 0.191. This is a simple, unadjusted recalculation from posted summary statistics. The standard deviations used for recalculation are approximate, inferred from the posted standard errors and group sizes rather than directly reported as standard deviations. Because the sponsor’s own analysis is available, its analysis takes precedence over a summary-statistic recalculation when describing the trial’s official inferential result. The recalculation remains useful as a check on the scale and uncertainty of the posted summary values.

A confidence interval describes a range of effect values compatible with the data and the method used to calculate it. Its width reflects precision: a wider interval indicates more uncertainty about the size and direction of the estimate. A confidence interval that includes zero is compatible with no average difference as well as with differences in either direction. It should not be interpreted as showing that all values within the interval are equally plausible, or as a probability statement about the true effect.

Why does over-dispersion matter?

For a continuous outcome, variability between participants affects how precisely a group mean and a group contrast can be estimated. Greater variation generally makes an estimate less precise when other features are unchanged. The posted arm spreads are standard errors, not participant-level standard deviations; the recalculated pooled standard deviations are approximate. General caution is needed when interpreting recalculations based on that conversion, particularly when the original analysis used a mixed model. For count outcomes, over-dispersion has a different meaning: the observed variation can exceed what a simple count model assumes, so uncertainty may be understated unless the model accommodates it. The primary endpoint is continuous, not a count endpoint.

How should p-values be read?

A p-value measures how unusual results at least as incompatible with a null hypothesis would be under that hypothesis and the specified analysis assumptions. It is not a measure of effect size, clinical importance, or the probability that the null hypothesis is true. The sponsor’s primary p-value is 0.206; the unadjusted recalculation gives 0.191. The registry does not report the planned decision threshold for the sponsor’s primary analysis, so the recalculated planning assumption of a two-sided significance level of 0.05 should not be mistaken for the trial’s documented analysis threshold.

The secondary recalculations are also unadjusted. When multiple outcomes are examined, the chance of at least one apparently notable result can increase if each is assessed without accounting for the family of tests. A nominal p-value for a secondary endpoint consequently carries less evidential weight than a prespecified, multiplicity-controlled analysis. The multiplicity plan is not reported in the registry record, so it is not possible to determine whether the sponsor used an adjustment or a hierarchical testing strategy.

Finally, the analysis population matters. The registry defines the full analysis set as randomized subjects with at least one post-baseline assessment, whether or not they received medication. That is the population stated for efficacy hypothesis tests. The record does not provide the number with missing Month 6 assessments, describe imputation, or state how participants without post-baseline data were handled. Those omissions limit assessment of how missing data might affect the estimates.

11. Confidence Intervals and Precision

The unadjusted recalculated primary difference is 1.4, with a confidence interval from -0.701 to 3.5. This interval crosses zero. It therefore encompasses no average difference and values on either side, including a negative difference and a positive difference. The result is not precise enough to identify the direction of the group contrast from the recalculation alone. The interval’s endpoints also make clear that a single point estimate should not be read as the only plausible description of the observed data.

The recalculation is based on the posted summary statistics and approximate standard deviations derived from standard errors. It is not the sponsor’s mixed-model confidence interval. The sponsor’s model-based interval and estimated contrast are not reported in the registry record, so the precision of the sponsor’s own treatment estimate cannot be assessed from the reported p-value alone. The sponsor’s p = 0.206 is a test result, not a substitute for an interval that shows the range of compatible effect sizes.

Small outcome groups can yield uncertain estimates, especially when individual measurements vary. The group sizes were 21 for azeliragon and 22 for placebo. These counts do not by themselves determine precision: the variation in scores and the analysis method also matter. The standard errors reported for the group summaries are 0.82 and 0.69, while the registry’s lack of a sponsor-model interval limits direct interpretation of model-based uncertainty.

Confidence intervals are conditional on their statistical method and assumptions. They do not account automatically for every source of uncertainty, including missing outcome data, model choice, or examining multiple endpoints. The registry record does not report enough detail to evaluate all of those issues. Thus the recalculated interval is informative about the uncertainty in a simple summary-statistic comparison, but it does not resolve the uncertainty surrounding the full trial analysis.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the listed figures are participants per arm, not a combined total. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect to detect equal to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for an illustration in which a study would have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column gives the corresponding number for a higher chance of detecting that effect. These are design calculations, not guarantees about what a future study would find. They do not say that the existing trial had an 80% or 90% probability of success, and they are not observed power.

The figures change with the assumed effect size. Planning for a smaller effect requires more participants per arm than planning for a larger effect, because smaller differences are harder to distinguish from random variation under otherwise unchanged assumptions. The displayed illustrations use fractions of the observed effect, which may be unstable when estimated in a small study; they should therefore be read as sensitivity scenarios rather than firm enrollment recommendations.

The stated assumptions do not document the original trial’s intended power, target effect, or planned analysis. The registry record does not report those original design choices, so the displayed planning illustrations cannot be used to infer why the study enrolled 43 participants or whether that enrollment was adequate for the protocol’s intended objective.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.400; pooled standard deviation σ = 3.500.
2. n = 2 × (1.96 + 0.842)² × 3.500² / 1.400² = 98.1, rounded up to 99 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 1.4                      # observed difference in means
sigma <- 3.50040485463346                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3980730)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 99 (80% power), 132 (90% power)
 75% of observed effect: n per arm = 175 (80% power), 234 (90% power)
 50% of observed effect: n per arm = 393 (80% power), 526 (90% power)
power.t.test: 99.1 
Simulated power at n = 99 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports that the sponsor used a Mixed Models Analysis for a superiority test on the primary outcome, with p = 0.206. It does not report the model-based treatment estimate, confidence interval, or additional model specifications. The sponsor’s result is therefore the primary reported inferential analysis, but the p-value alone does not convey the estimated magnitude or precision of the group difference.

The simple recalculation from posted summaries gives a mean difference of 1.4, a confidence interval from -0.701 to 3.5, and an unadjusted p-value of 0.191. This calculation uses the displayed arm summaries and approximate standard deviations; it is not a reconstruction of the mixed model. The two p-values should not be treated as interchangeable because they come from different analyses and may rely on different information and assumptions.

The registry does not flag a discrepancy between the sponsor’s reported result and the recalculation. That does not make the recalculation the official result: it remains a secondary check based on limited summary information. In interpreting the trial, the sponsor’s mixed-model test takes precedence as the reported analysis, while the recalculation helps illustrate the uncertainty apparent in the posted arm summaries. The absent model estimate and interval prevent a fuller comparison of their effect estimates and precision.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes or performs several statistical tests. If each test is interpreted independently without adjustment, the chance of at least one apparently notable result can rise across the set. The registry lists a primary endpoint and multiple secondary outcomes, and the posted results include several secondary comparisons. Their unadjusted p-values should therefore be interpreted as nominal results rather than as evidence that has necessarily been protected against the full set of comparisons.

The registry record does not report whether the protocol specified a multiplicity adjustment, a hierarchy of outcomes, or another approach for controlling the interpretation of multiple tests. It also does not report a statistical analysis plan that would establish which outcomes were confirmatory, how decisions were to be made, or whether analyses changed after study initiation. In the absence of that information, the secondary outcomes carry less weight than a single prespecified primary test interpreted under a documented plan.

The stated analysis population is the full analysis set: randomized participants, regardless of whether they received study medication, who had at least one post-baseline assessment. The registry states that this population was used for efficacy hypothesis tests. It does not give the number of randomized participants excluded from an endpoint analysis, the number lacking a Month 6 measure, or the reasons for missing observations. The outcome group counts are 21 and 22, but the record does not explain whether they represent all randomized participants or only those with usable endpoint data.

The record also does not describe an imputation method, a sensitivity analysis for missing data, or the assumptions used by the mixed model for incomplete repeated measurements. Missingness can affect a comparison if the availability of measurements is related to outcomes or differs between groups. Without the needed details, the direction or size of any such effect cannot be determined.

These omissions do not prove that the analyses were inappropriate; they mean that key choices cannot be evaluated from the registry record. The sponsor’s primary result can be reported as stated, but the broader inferential context—including multiplicity and missing-data sensitivity—remains unclear.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gait disturbance (4.8%).

The posted safety counts show 1 serious adverse event among 21 participants at risk in the azeliragon group and 0 among 22 participants at risk in the placebo group. The registry lists gait disturbance as the top serious adverse-event term, at 4.8%. It does not provide enough detail in the record to attribute that term to a particular treatment group from the information. Deaths were recorded as 0 in both groups.

Other adverse events were recorded for 9 of 21 participants at risk with azeliragon and 13 of 22 at risk with placebo. These are participant counts, not measures of event severity or duration. Counts alone do not establish whether an event was caused by study treatment, and the registry record does not provide the detail needed to assess timing, recurrence, or the clinical circumstances of each event.

The group sizes are small, so the counts should be read descriptively rather than as precise estimates of comparative safety. A zero count does not demonstrate that an event cannot occur, and a difference in counts does not by itself establish a treatment-related difference. The safety figures are limited to the adverse-event information posted in the registry record.

17. What the Result Does, and Does Not, Mean

The posted primary results describe a small randomized comparison of azeliragon and placebo over Part 1’s 6-month treatment period. The azeliragon group’s least-squares mean ADAS-cog14 change was 1.8, and the placebo group’s was 0.4. The scale assigns higher scores to greater cognitive impairment. The sponsor’s mixed-model superiority test reported p = 0.206, while the unadjusted summary-statistic recalculation gave a mean difference of 1.4 and a confidence interval that includes zero.

These results do not establish a clear difference between the groups on the primary endpoint. They also do not establish that the groups were equivalent: a non-significant test or interval including zero is not proof that the true difference is exactly zero. The estimates remain compatible with a range of possible differences, and the sponsor’s model-based estimate and confidence interval are not reported in the registry record.

The secondary results offer additional measurements but do not settle the primary uncertainty. Their pattern is mixed, the MMSE numerical result is not reported, and the registry does not state how multiplicity was handled. Safety counts are descriptive and cannot by themselves establish whether events were caused by treatment. The trial’s terminated status is recorded, but the reason is not reported in the registry record, so it should not be used to infer the interpretation of the results.

As a result, the posted information supports a cautious description of observed group summaries and reported analyses, not a medical recommendation or a definitive judgment about azeliragon. The findings apply to this study population and the recorded Part 1 assessment; the record does not establish how they would generalize to other populations, treatment durations, or settings.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a hypothesis test answer different questions. The arm summaries give a numerical description of average change, while the sponsor’s reported p-value addresses a statistical test under its model. The primary estimate and the uncertainty around a recalculated contrast help show why a single reported result should not be read without considering precision.

It also shows the importance of distinguishing a sponsor’s analysis from a simple recalculation using posted summaries. The mixed-model p-value is the reported primary test, whereas the recalculation is based on arm-level means and approximate standard deviations. The latter can provide a useful check, but it cannot reproduce unreported model details or replace the sponsor’s analysis.

The secondary outcomes and safety counts raise related interpretive issues. Several outcomes can create multiplicity concerns, and unadjusted secondary findings deserve less weight when the analysis plan is unavailable. Small participant counts make safety comparisons especially descriptive. Clear reporting of analysis populations, missing-data methods, multiplicity plans, and effect estimates with confidence intervals would make it easier to assess these results.

Finally, the record states that the study was terminated but does not report why. That status is part of the study context, but it does not by itself explain the results or establish the reason for the available amount of data. Separating recorded details from unreported context is central to a statistically careful reading.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Interpretation is limited by the small posted outcome groups: 21 participants for azeliragon and 22 for placebo. The primary recalculated interval includes zero and is compatible with differences in either direction. The sponsor’s model-based estimate and confidence interval are not reported, leaving the magnitude and precision of the official model-based treatment contrast unclear.

The posted recalculation uses approximate standard deviations inferred from standard errors. It is therefore not a direct reproduction of the sponsor’s mixed-model analysis. The registry does not report details of the model specification, the treatment of repeated observations, or sensitivity analyses. Those omissions restrict assessment of whether the simple recalculation and sponsor analysis target precisely the same quantity.

The record does not describe the original sample-size justification, planned power, or target effect. The displayed planning illustrations are based on the observed effects and cannot establish whether the actual enrollment was adequate for the original study objective. The registry also does not explain the terminated status, so no reason for termination can be inferred.

Further limitations include unreported missing-data counts and methods, no reported multiplicity plan, and the absence of numerical MMSE results. The secondary outcomes are therefore difficult to place within a prespecified inferential framework. The safety counts have limited precision and do not establish causality. These constraints mean the available results are best treated as descriptive and uncertain rather than as a complete account of the trial’s evidence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Azeliragon in Patients With Mild Alzheimer's Disease and Impaired Glucose Tolerance — NCT03980730.
• Registry record last updated 2022-01-21; status last verified 2021-12.
• Results first posted 2022-01-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a Phase 2 randomized, double-blind, placebo-controlled, multicenter parallel-group study of azeliragon in people with mild Alzheimer’s disease and impaired glucose tolerance. It lists quadruple masking, enrollment of 43, and a terminated status. Part 1 compared oral azeliragon 5mg once daily with matching placebo for 6 months.

The primary outcome was change from baseline to Month 6 in ADAS-cog14. The sponsor reported a mixed-model superiority test with p = 0.206. A summary-statistic recalculation gave a mean difference of 1.4 with a confidence interval including zero. Secondary results were mixed, and the registry does not report numerical MMSE results or a multiplicity plan. Safety counts included 1 serious adverse event with azeliragon and 0 with placebo; deaths were 0 in both groups.

The registry record does not report the reason for termination, the original sample-size justification, or key details of missing-data and multiplicity handling.