A Study of LY3202626 on Disease Progression in Participants With Mild Alzheimer's Disease Dementia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of LY3202626 on Disease Progression in Participants With Mild Alzheimer's Disease Dementia (NCT02791191), a randomized phase 2 study. The primary outcome is Change From Baseline in ¹⁸F-AV-1451 Positron Emission Tomography (PET) Standard Uptake Value Ratio (SUVr) at 52 Weeks.

2. Clinical Question

The study's stated purpose was to evaluate safety and the effect of LY3202626 on brain tau in participants with mild Alzheimer's disease dementia. ¹⁸F-AV-1451 PET was used to assess tau-related signal, and the primary outcome was change in its standard uptake value ratio (SUVr) from baseline to Week 52. The registry describes comparisons of each dose with placebo, rather than a direct comparison between the doses.

The posted endpoint means were 0.02 for 3 mg, 0.03 for 12 mg, and 0.01 for placebo. These are changes in SUVr, not a direct measure of day-to-day function or a clinical diagnosis. The registry also lists cognitive and functional measures as secondary outcomes. Those measures can provide additional context, but they do not change what the primary endpoint was designed to measure.

The question is therefore narrow: whether the observed PET measure differed across randomized groups at the specified assessment. The posted estimates and analyses describe the data available for the endpoint population. They do not, by themselves, establish a clinical benefit, explain why the study was terminated, or show what the result would have been in a different population or under a different follow-up plan.

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group study sponsored by Eli Lilly and Company. Participants were assigned to 3 mg LY3202626, 12 mg LY3202626, or placebo. The registry describes each regimen as an oral dose taken once daily for 52 weeks. A parallel design compares groups assigned to different study regimens over the same study period; randomization is intended to support fair comparisons by allocating treatment assignment through a chance process.

The registry lists 316 participants as enrolled. That overall enrollment figure should not be confused with the number contributing to a particular outcome. For the primary PET endpoint, the registry specifies an analysis population that had received at least one dose and had both a baseline and at least one post-baseline scan. The posted primary outcome groups contain 15 participants for 3 mg, 15 for 12 mg, and 11 for placebo. The registry does not explain in this record why the endpoint groups are smaller than the enrollment figure, or provide enough information to characterize all reasons for missing endpoint data.

The trial is marked terminated. The recorded start date is 2016-06-16, and the primary completion date is 2018-07-02. The registry record does not report a reason for termination in the registry record for this analysis, so no inference about the reason is warranted.

Triple masking indicates that the registry categorized the study as masked across three roles, but the specific roles are not reported in the registry record. The allocation process beyond its randomized classification, concealment procedures, and any stratification factors are also not reported in the registry record. The record identifies a parallel model and the assigned regimens, but does not establish additional details about adherence, treatment changes, or follow-up procedures beyond the stated endpoint time frame.

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: All participants who received at least one dose of study drug, and have baseline and at least one post-baseline scan.

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.

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in ¹⁸F-AV-1451 Positron Emission Tomography (PET) Standard Uptake Value Ratio (SUVr) at 52 Weeks, measured over Baseline, Week 52.

The primary endpoint was change from baseline in ¹⁸F-AV-1451 PET standard uptake value ratio (SUVr) at Week 52. The tracer is used to assess tau-related signal in the brain, and the study described this outcome as a pharmacodynamic measure. In general, a pharmacodynamic endpoint assesses a biological response associated with a treatment; it is not automatically a measure of how a participant feels, functions, or survives.

SUVr expresses PET signal as a ratio, allowing the study to quantify the tracer signal under a defined imaging and analysis approach. The registry's primary-endpoint description says that the SUVr was modeled using analysis of covariance (ANCOVA), with treatment dose as a fixed categorical effect and baseline Tau PET SUVr and age at baseline as continuous fixed covariates. This adjustment is intended to compare treatment groups while accounting for specified baseline characteristics. It does not mean that the posted group means alone reproduce the adjusted model.

The outcome is useful for the research question because it targets the study's stated interest in brain tau and can register a biological change over the study period. Its interpretation remains specific to the PET measure, the endpoint population, and the Week 52 assessment. A difference in SUVr would not by itself establish a difference in clinical progression, while a lack of clear separation in the posted estimates does not establish equivalence. The registry record does not report a threshold for a clinically important SUVr change, so the clinical meaning of a particular numerical difference is not established in the record.

7. Results Posted in the Registry

• 3 mg LY3202626: mean 0.02 versus 0.01 on control; difference 0.01 (95% CI -0.04 to 0.06), standardized effect d = 0.17; z-test p = 0.703.
• 12 mg LY3202626: mean 0.03 versus 0.01 on control; difference 0.02 (95% CI -0.03 to 0.07), standardized effect d = 0.33; z-test p = 0.446.

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.

Change From Baseline on the 13-item Alzheimer's Disease Assessment Scale-Cognition (ADAS-Cog₁₃)

• 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:
  • 3 mg LY3202626: mean 3.05 versus 2.97 on control; difference 0.08 (95% CI -3.96 to 4.12), standardized effect d = 0.01; z-test p = 0.969.
  • 12 mg LY3202626: mean 1.88 versus 2.97 on control; difference -1.09 (95% CI -5.03 to 2.85), standardized effect d = -0.19; z-test p = 0.588.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 3 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 12 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline on the Alzheimer's Disease Cooperative Study-Instrumental Activities of Daily Living Inventory (ADCS-iADL)

• 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:
  • 3 mg LY3202626: mean -3.97 versus -7.32 on control; difference 3.35 (95% CI -0.42 to 7.12), standardized effect d = 0.62; z-test p = 0.082.
  • 12 mg LY3202626: mean -4.63 versus -7.32 on control; difference 2.69 (95% CI -0.95 to 6.33), standardized effect d = 0.50; z-test p = 0.147.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 3 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 12 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline on the Integrated Alzheimer's Disease Rating Scale (iADRS)

• 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:
  • 3 mg LY3202626: mean -6.01 versus -10.32 on control; difference 4.31 (95% CI -1.54 to 10.16), standardized effect d = 0.52; z-test p = 0.149.
  • 12 mg LY3202626: mean -6.45 versus -10.32 on control; difference 3.87 (95% CI -1.75 to 9.49), standardized effect d = 0.47; z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 3 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 12 mg LY3202626 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists cognitive and functional measures among its secondary outcomes, including ADAS-Cog₁₃, ADCS-iADL, and iADRS. The posted results also include secondary safety, imaging, pharmacokinetic, and plasma amyloid measures. Eight secondary outcomes are posted, and the record lists 30 analyses across outcomes. Those results broaden the description of the study but do not redefine the primary endpoint, which was tau PET SUVr change at Week 52.

Across the posted cognitive and functional comparisons, the results do not form a consistent pattern of clear separation from placebo. Some estimated differences favor one group numerically, while the corresponding uncertainty remains substantial. The sponsor's analyses use mixed model repeated measures for ADAS-Cog₁₃ and ANCOVA for ADCS-iADL and iADRS. The unadjusted recalculations are not equivalent to those sponsor models and should be read as secondary descriptive checks.

Secondary outcomes can help assess whether patterns across biological, cognitive, and functional measures align, but a coherent interpretation requires attention to the different scales, models, and missing data. A result on a cognitive or functional scale cannot be treated as confirmation of a PET result simply because the direction appears similar. Conversely, a secondary outcome that differs numerically does not overturn the primary analysis.

Unadjusted secondary results carry less weight because many outcome and treatment comparisons create more opportunities for chance findings. The registry record does not report a multiplicity-adjustment strategy for these results. Without a stated plan, individual secondary p-values should be treated as exploratory rather than as independent confirmatory evidence. The overall pattern is more informative than selecting one isolated estimate, but it remains limited by the available analysis details and endpoint group sizes.

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

• Percentage of Participants With Emergent Magnetic Resonance Imaging (MRI) Findings
• Percentage of Participants With Amyloid-Related Imaging Abnormalities (ARIA)
• Percentage of Participants With Suicidal Ideation and Behaviors Assessed by the Columbia Suicide Severity Rating Scale (C-SSRS) Scores
• Pharmacokinetics (PK): Area Under the Plasma Concentration-Time Curve at Steady State (AUC [T,SS]) of LY3202626
• Change From Baseline in Plasma Amyloid Beta Aβ₁-₄₀, ₁-₄₂, and 1-x Concentration
• Change From Baseline on the 13-item Alzheimer's Disease Assessment Scale-Cognition (ADAS-Cog₁₃)
• Change From Baseline on the Alzheimer's Disease Cooperative Study-Instrumental Activities of Daily Living Inventory (ADCS-iADL)
• Change From Baseline on the Integrated Alzheimer's Disease Rating Scale (iADRS)

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the reported trial analysis from the simple recalculations. The points below describe general concepts and then relate them to the methods named in the registry record.

What does a group mean describe?

For a continuous outcome such as change in SUVr, a mean is an average of the observed values in a group. It gives a compact description of the group's central tendency, but it does not show the range of individual responses or whether the distribution is symmetric. The posted primary outcome gives a mean and standard deviation for each dose group and placebo. The standard deviation describes variation among the observations; it is not the same thing as uncertainty in the estimated mean.

The primary groups have mean changes of 0.02, 0.03, and 0.01 for 3 mg, 12 mg, and placebo, respectively. The posted standard deviations are 0.04, 0.04, and 0.08. The observed spread is therefore not identical across groups. With modest endpoint group sizes, estimates of both group means and between-group differences can be imprecise.

What does a mean difference represent?

A mean difference contrasts the average outcome in a treatment group with the average in the placebo group. The recalculated differences are 0.01 for 3 mg versus placebo and 0.02 for 12 mg versus placebo. A positive difference means the treatment-group mean change is numerically greater than the placebo mean change under the subtraction order used in the recalculation. The sign alone does not establish whether the result is clinically favorable; that depends on the outcome's interpretation and the study question.

These recalculations are unadjusted comparisons based on posted summary statistics. They do not reproduce the sponsor's ANCOVA. The ANCOVA compares treatment groups while accounting for baseline Tau PET SUVr and age at baseline, as described in the primary endpoint record. Adjustment can alter an estimated treatment contrast or its uncertainty, particularly when baseline measures are associated with the outcome. The registry does not provide the adjusted estimates, so their size and direction cannot be compared directly with the recalculated differences.

Why use ANCOVA?

In general, analysis of covariance combines a group comparison with adjustment for continuous covariates. Including a baseline measure can account for initial differences in the outcome measure and can improve precision when that baseline measure predicts follow-up values. Age at baseline is another specified covariate in this trial's endpoint model. Treatment dose is represented as a fixed categorical effect, allowing the model to estimate group differences rather than assuming dose has a linear effect.

The primary description identifies the covariates and the model family, but it does not report all details needed to reproduce the analysis. For example, the registry record does not report the complete model specification, handling of missing scans within the model, diagnostic checks, or the exact approach to any multiplicity. Those details should not be inferred from the word ANCOVA alone.

How should p-values be read?

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of a difference. The sponsor-reported primary p-values are 0.418 and 0.231. The unadjusted recalculated p-values are 0.703 and 0.446. These should be interpreted alongside the effect estimates and their uncertainty, not as stand-alone measures of evidence.

The primary endpoint record labels the sponsor's comparisons as superiority analyses. A superiority test asks whether evidence supports a difference in a specified direction or, depending on its implementation, any difference. It does not test whether treatments are equivalent. Demonstrating equivalence would require an equivalence margin and a suitable analysis, neither of which is reported in the registry record.

Why do estimates and p-values differ across analyses?

The recalculated comparisons use the posted means, variation estimates, and group sizes to make simple unadjusted comparisons. The sponsor's primary analysis uses ANCOVA and adjusts for baseline Tau PET SUVr and age. The analyses can therefore produce different p-values without either being a transcription error. They target different model-based contrasts and may use different information or assumptions. The recalculated interval estimates are not replacements for missing sponsor-reported adjusted intervals.

For the recalculated primary comparisons, both intervals include zero. In general, a confidence interval gives a range of effect estimates compatible with the data under the interval's method and assumptions. Its width reflects precision: a wider interval is less informative about the size of the underlying difference. A confidence interval does not assign probability to a fixed effect after the data have been observed. The registry's adjusted confidence intervals are not reported.

Why can over-dispersion matter?

Over-dispersion is a general concern when observed variation is greater than a model assumes. In such cases, a model can understate uncertainty if its variance assumptions are too restrictive. For continuous outcomes, the standard deviation helps describe observed variation; for other outcome types, model-specific dispersion assumptions may be important. The registry entries do not identify over-dispersion as a problem in this trial, so it should not be claimed that it occurred. The concept matters as a general reminder that uncertainty depends on whether the model represents the data's variability adequately.

The secondary outcomes use different measures and analysis methods, including mixed model repeated measures and ANCOVA. Those methods can use repeated observations or adjust for covariates, but the registry record does not provide enough detail to reconstruct every model. The recalculated secondary comparisons are simple summaries, not substitutes for those longitudinal or adjusted analyses. Where the posted analysis method differs from the recalculation, the sponsor's model is the one that corresponds to the registry's reported analysis.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate identifies the plausible size of a group difference. The recalculated primary intervals for both dose-versus-placebo comparisons include zero. This means the summaries do not pin down a clear direction of difference. Their breadth also indicates that the point estimates should not be read as precise measurements of the underlying treatment contrasts.

The reported primary group means are close in numerical terms, but closeness of point estimates is not proof of equivalence. The endpoint groups include 15 participants for each LY3202626 dose and 11 for placebo. Such group sizes can leave substantial uncertainty, particularly when variability is present. The posted standard deviations are 0.04, 0.04, and 0.08, respectively. These describe observed spread in the endpoint groups, not the precision of the sponsor's adjusted estimates.

The recalculated intervals are unadjusted and are not the intervals from the registry's ANCOVA. The registry record does not post adjusted confidence intervals or identify the confidence level for the sponsor analysis. Consequently, the recalculated intervals can help illustrate uncertainty from the summary statistics, but they cannot be used as a direct report of the sponsor's model-based precision.

More generally, a confidence interval is a range generated by a statistical procedure that, under its assumptions, is designed to cover the underlying parameter at a specified long-run rate. Its interpretation depends on the method and assumptions. A wide interval is compatible with a broader range of effects; a narrow interval gives a more precise estimate. Neither width nor inclusion of zero alone settles clinical importance. The registry record does not report a threshold for a clinically meaningful SUVr difference, so the precision of these estimates cannot be translated into a judgment about clinical relevance.

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 participants per arm, not total events. They illustrate the group size a hypothetical future comparison might require under the stated calculation assumptions. They are not the original design targets for this trial; the trial's own sample-size assumptions and justification are not reported in the registry record.

The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its starting point, then considers planning for 100%, 75%, or 50% of that observed effect. The 80% power column gives the participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect is real and the model assumptions hold. The 90% power column gives the corresponding group size for a 90% chance.

Smaller effects require more participants to detect under otherwise similar assumptions. This is why the planning illustrations increase when the target is 75% or 50% of the observed effect. In comparisons where the observed difference is especially small, the resulting illustrations can become very large. Such values are not recommendations; they are sensitive to the observed effect, which can itself be unstable in small groups.

These are planning illustrations, not observed power. They do not tell whether the completed study had a particular probability of success, and they do not establish that an effect is real. The figures also do not account for design features or analysis choices beyond the stated assumptions. The registry record does not report the original design assumptions, so these calculations should be kept separate from the study's actual planning rationale.

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 = 0.010; pooled standard deviation σ = 0.060.
2. n = 2 × (1.96 + 0.842)² × 0.060² / 0.010² = 565.1, rounded up to 566 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 <- 0.01                      # observed difference in means
sigma <- 0.06                     # 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(2791191)
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 = 566 (80% power), 757 (90% power)
 75% of observed effect: n per arm = 1,005 (80% power), 1,345 (90% power)
 50% of observed effect: n per arm = 2,261 (80% power), 3,027 (90% power)
power.t.test: 566.1 
Simulated power at n = 566 per arm: 0.797 (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's own primary analyses compare each LY3202626 dose with placebo using ANCOVA. The reported p-values are 0.418 for 3 mg versus placebo and 0.231 for 12 mg versus placebo. The record does not post the corresponding adjusted effect estimates or confidence intervals.

The recalculated comparisons are simple unadjusted analyses of posted summary statistics. They estimate mean differences of 0.01 for 3 mg versus placebo and 0.02 for 12 mg versus placebo, with p-values of 0.703 and 0.446, respectively. The recalculated intervals include zero. These results are not intended to replace the ANCOVA, which adjusts for treatment dose, baseline Tau PET SUVr, and age at baseline according to the endpoint description.

The p-values differ because the recalculation and sponsor analysis do not use the same model. An adjusted analysis can account for covariates and may use information differently from a summary-statistic comparison. The registry does not report enough model output to reproduce the sponsor's estimates or explain the precise numerical difference between the analyses. Because the discrepancy flag is false, there is no recorded conflict that would displace the sponsor's own analysis. The sponsor's ANCOVA is the primary registry analysis; the recalculation is a supplementary, unadjusted check.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, treatment comparisons, time points, or analysis choices. Even when each individual test is conducted carefully, conducting many tests increases the chance that at least one result will appear notable by chance. A prespecified strategy can control how results are interpreted, for example by defining a testing order or adjusting significance criteria. The registry lists 30 analyses and multiple secondary outcomes, but a multiplicity strategy is not reported in the registry record.

The primary outcome compares 3 mg with placebo and 12 mg with placebo. The registry identifies both as superiority analyses, but does not report whether the primary comparisons were handled within a hierarchy or whether any adjustment was planned. Accordingly, the reported p-values should be interpreted with the model and stated primary question in mind, without assuming an unreported testing procedure.

Missing data are also relevant. The primary endpoint population required at least one dose, a baseline scan, and at least one post-baseline scan. The posted primary groups contain fewer participants than the registry's enrollment figure. The record does not explain all differences between enrollment and endpoint analysis, provide a complete accounting of missing scans, or state the assumptions used for any missing endpoint data. It also does not describe sensitivity analyses for alternative missing-data assumptions.

The analysis population is defined for the primary endpoint, but that definition is not the same as a full intention-to-treat analysis of every randomized participant. The registry record does not report enough detail to determine how all randomized participants were handled across endpoints, whether exclusions occurred after randomization, or whether analyses followed the originally assigned groups in every case. These are material questions because exclusion or missingness can affect comparability if related to prognosis or treatment experience.

The ANCOVA method and primary covariates are described, but a complete statistical analysis plan is not reported in the registry record. Interim analyses, stopping rules, sample-size justification, model diagnostics, and the detailed handling of missing values are not reported in the registry record. Their absence from this record does not establish that such plans or procedures did not exist; it means they cannot be assessed from the registry information analyzed.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (1.8%), coronary artery disease (1.8%), duodenal ulcer (1.8%), gastrointestinal haemorrhage (1.8%), small intestinal obstruction (1.8%).

The safety record reports serious adverse events by treatment group and gives the number at risk and number affected. For 3 mg LY3202626, 55 participants were at risk and 10 had a serious adverse event. For 12 mg, 127 were at risk and 8 were affected. For placebo, 133 were at risk and 10 were affected. Deaths were recorded as 0 in each group.

These counts are not a complete comparison of all possible harms. They describe serious adverse events as recorded in the registry, using the stated at-risk groups. The record also lists serious adverse event terms with a reported percentage of 1.8% for each of angina pectoris, coronary artery disease, duodenal ulcer, gastrointestinal haemorrhage, small intestinal obstruction, and cystitis. The registry entries do not specify enough detail to establish whether the listed terms are mutually exclusive or to infer a total number of events by adding them.

Differences in group sizes and exposure, event definitions, follow-up, and chance can affect interpretation of safety counts. The registry record does not provide a full account of event timing, severity beyond the serious classification, relatedness, or all non-serious adverse events in the registry record for this analysis. These counts therefore describe the posted serious-event information but do not by themselves establish comparative safety.

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

The primary results show that the posted mean change in tau PET SUVr was 0.02 in the 3 mg group, 0.03 in the 12 mg group, and 0.01 in the placebo group. The sponsor's ANCOVA comparisons reported p-values of 0.418 and 0.231. The registry does not provide adjusted effect estimates or adjusted confidence intervals. The unadjusted recalculations give small mean differences, and their intervals include zero.

These findings do not establish a clear difference between either LY3202626 dose and placebo on the primary PET endpoint. They also do not establish equivalence or prove that the true effect is exactly zero. The endpoint groups are limited in size, and the recalculated intervals are compatible with a range of possible underlying differences. The registry does not report a clinically meaningful threshold for a change in SUVr, so the clinical importance of a particular numerical contrast cannot be determined from this record.

The primary measure is a biological imaging endpoint. It does not directly measure symptoms, daily functioning, or the overall course of Alzheimer's disease. A result on this endpoint cannot alone show whether participants experienced a meaningful change in their lives. The secondary cognitive and functional outcomes provide related but distinct information, and their results should not be combined into a single conclusion without considering their own scales, models, and multiplicity.

The safety counts report serious adverse events and deaths, but they do not capture every aspect of risk or establish a treatment effect on safety. Likewise, the trial's terminated status is a registry classification; the reason for termination is not reported in the registry record. Taken together, the posted results describe the evidence available for this study, not a general conclusion about all participants with Alzheimer's disease dementia, all doses, or other treatment settings.

18. Why This Trial Matters Statistically

This study is statistically instructive because it places a biological imaging endpoint at the center of a randomized comparison while also posting cognitive, functional, and safety outcomes. It highlights the distinction between a biomarker-oriented measure and outcomes that more directly reflect cognition or daily activities. That distinction matters when translating a statistical contrast into a claim about clinical progression.

The record also illustrates why analysis populations and model descriptions deserve close attention. Enrollment is 316, while the primary endpoint results are reported for smaller groups meeting a scan-based population definition. The ANCOVA description identifies baseline Tau PET SUVr and age as covariates, but the registry does not provide the adjusted estimates or the complete model output. Readers can therefore distinguish the sponsor's specified approach from a simple summary-statistic recalculation, but cannot fully reproduce the primary analysis from the posted information.

Another important lesson is that non-significant results do not demonstrate no effect. The estimates, p-values, and intervals must be considered together, and the uncertainty in the recalculated comparisons is substantial. At the same time, an observed numerical difference should not be presented as a confirmed effect when the sponsor's analysis does not show clear separation and the registry does not report an equivalence design or clinically meaningful threshold.

Finally, the record contains multiple outcomes and analyses. Without a reported multiplicity strategy, secondary findings require cautious interpretation. The study therefore provides a practical example of how randomized design, covariate adjustment, endpoint choice, precision, missingness, and multiple testing jointly shape what can reasonably be concluded from clinical-trial results.

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.

Several limitations are specific to the information posted for this trial. First, the primary endpoint analysis groups are much smaller than the enrollment figure, and the registry does not provide a full accounting of why participants are absent from the endpoint results. The defined population required baseline and post-baseline PET scans, so the reported endpoint pertains to participants meeting that scan criterion rather than necessarily to every randomized participant.

Second, the sponsor-reported ANCOVA p-values are available, but adjusted effect estimates and confidence intervals are not. The unadjusted recalculations cannot fill that gap because they do not adjust for baseline Tau PET SUVr and age. Their intervals and p-values should not be mistaken for outputs from the sponsor's model.

Third, the registry record does not report the original sample-size justification, detailed missing-data methods, interim analyses, or a full multiplicity plan. These omissions restrict evaluation of whether the completed analysis followed all planned procedures and how sensitive results might be to alternative assumptions. The reason for the terminated status is also not reported in the registry record.

Finally, the primary outcome is a PET SUVr measure, and the record does not identify a threshold for a clinically meaningful change. The findings therefore have limits both in statistical precision and in the clinical interpretation of a numerical biomarker contrast. Secondary outcomes involve different measures and models, and the multiple analyses make isolated findings less persuasive without a documented adjustment strategy.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of LY3202626 on Disease Progression in Participants With Mild Alzheimer's Disease Dementia — NCT02791191.
• Registry record last updated 2021-04-19; status last verified 2021-03.
• Results first posted 2021-04-19.
• 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, triple-masked, parallel-group study of 3 mg or 12 mg LY3202626 versus placebo in mild Alzheimer's disease dementia. Each regimen was taken orally once daily for 52 weeks. Enrollment was 316, and the study is marked terminated.

The primary endpoint was change from baseline in ¹⁸F-AV-1451 PET SUVr at Week 52. Sponsor-reported ANCOVA p-values were 0.418 for 3 mg versus placebo and 0.231 for 12 mg versus placebo. The registry does not post adjusted effect estimates or confidence intervals. Unadjusted recalculations show small mean differences with intervals that include zero.

The registry posts secondary cognitive, functional, imaging, pharmacokinetic, amyloid, and safety outcomes. Interpretation is limited by small primary endpoint groups, incomplete reporting of missing-data and multiplicity methods, and the absence of the trial's original sample-size justification in the registry record.