BI 425809 in Patients With Cognitive Impairment Due to Alzheimer's Disease.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BI 425809 in Patients With Cognitive Impairment Due to Alzheimer's Disease. (NCT02788513), a randomized phase 2 study. The primary outcome is Change From Baseline in Alzheimer's Disease Assessment Scale-Cognitive Subscale 11 Item (ADAS-Cog11) Total Score After 12 Weeks of Treatment.

2. Clinical Question

3. Trial Design

This phase 2 study, NCT02788513, evaluated BI 425809 in patients with cognitive impairment due to Alzheimer’s disease. The registry record describes a multi-centre, randomized, double-blind, parallel-group controlled study, with a 12-week treatment period and placebo as the comparator. Participants were assigned to 2 mg, 5 mg, 10 mg or 25 mg BI 425809, or placebo. The registry record lists 611 as the enrollment and marks the study completed. Its recorded start date is 2016-08-11, and its primary completion date is 2019-09-12.

The primary outcome was change from baseline in ADAS-Cog11 total score after 12 weeks. The recorded assessment times are day 1, identified as visit 2 and baseline, and day 85, identified as the end of trial. Secondary outcomes were change from baseline in the ADCS-ADL score and the CIBIC+ score after 12 weeks. The registry record lists three outcome measures and 18 analyses, though only two secondary outcomes are posted in the available record.

The full analysis set was the efficacy population. It included randomized patients who received at least one dose of trial medication and had a baseline and at least one corresponding post-baseline on-treatment efficacy assessment for any efficacy endpoint. This definition is narrower than simply being randomized: treatment exposure and evaluable efficacy information were also required. The registry record does not report the original sample-size justification, planned interim analyses or the study’s original detailed design assumptions.

Five groups appear in the primary outcome results: the four dose groups and placebo. The arm-level analysis counts vary by outcome, as the efficacy population definition depends on available assessments. Enrollment should therefore not be treated as the denominator for every endpoint or analysis. The reported design establishes the comparison structure, but the registry record does not report further details about recruitment, allocation concealment or how masking was maintained.

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.

Before assignment: Subjects were screened prior to participation and attended a specialist site which ensured that they strictly met all inclusion/exclusion criteria. Subjects were not to be allocated to a treatment group if any of the criteria were violated. One subject was randomized by error via Interactive Response Technology (IRT) but never took a drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): all randomised patients who were treated with at least one dose of trial medication and had a baseline and at least one corresponding post-baseline on-treatment efficacy assessment for any efficacy endpoint. FAS was used for efficacy analyses.

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: Treated set (TS): the TS included all patients treated with at least one dose of trial medication. Patients in the treated set were analysed based on the actual treatment received at the randomisation. The TS was used for safety analyses.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Alzheimer's Disease Assessment Scale-Cognitive Subscale 11 Item (ADAS-Cog11) Total Score After 12 Weeks of Treatment, measured over On day 1 (visit 2, baseline) and day 85 (end of trial).

The primary endpoint was change from baseline in the total ADAS-Cog11 score after 12 weeks of treatment. ADAS-Cog11 is an 11-item cognitive subscale that objectively assesses memory, language, orientation and praxis. The total score ranges from 0 to 70, and lower scores indicate less severe impairment. Under the registry’s stated direction, a negative change indicates improvement from baseline.

Change from baseline expresses the difference between an individual’s starting score and a later assessment, and the reported arm-level results summarize those changes with means and standard deviations. This approach focuses on movement over the treatment period rather than only on the score at the end. It can be informative when participants begin at different levels, although how baseline information is handled in the model also matters. The primary analysis used a repeated-measures model with baseline and baseline-by-visit terms among its covariates.

A cognitive scale is used to turn several assessed domains into a structured outcome that can be compared across randomized groups. The endpoint alone does not capture every aspect of daily functioning or clinical experience; the registry lists ADCS-ADL and CIBIC+ as secondary outcomes. The interpretation of a group mean change also depends on its uncertainty, the analysis model and the comparison being made. The registry record does not report a threshold for a clinically important change, so the posted score differences cannot be classified against such a threshold using this record alone.

7. Results Posted in the Registry

• 2 mg BI 425809: mean 0.03 versus 0.14 on control; difference -0.11 (95% CI -1.36 to 1.13), standardized effect d = -0.02; z-test p = 0.860.
• 5 mg BI 425809: mean 0.17 versus 0.14 on control; difference 0.04 (95% CI -1.16 to 1.23), standardized effect d = 0.01; z-test p = 0.952.
• 10 mg BI 425809: mean 0.70 versus 0.14 on control; difference 0.56 (95% CI -0.62 to 1.74), standardized effect d = 0.12; z-test p = 0.350.
• 25 mg BI 425809: mean -0.17 versus 0.14 on control; difference -0.31 (95% CI -1.46 to 0.84), standardized effect d = -0.07; z-test p = 0.595.

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 in the Alzheimer's Disease Cooperative Study/Activities of Daily Living (ADCS-ADL) Score After 12 Weeks of Treatment

• 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 deviations.
• Result:
  • 2 mg BI 425809: mean 0.28 versus 0.26 on control; difference 0.02 (95% CI -1.52 to 1.57), standardized effect d = 0.00; z-test p = 0.978.
  • 5 mg BI 425809: mean 0.58 versus 0.26 on control; difference 0.32 (95% CI -1.10 to 1.73), standardized effect d = 0.06; z-test p = 0.661.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2 mg BI 425809 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 5 mg BI 425809 and the control. The interval gives the range of effects that remain compatible with the data.

Clinician's Interview-Based Impression of Change (CIBIC+) Score After 12 Weeks of Treatment

• 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 deviations.
• Result:
  • 2 mg BI 425809: mean 4.00 versus 4.08 on control; difference -0.08 (95% CI -0.31 to 0.15), standardized effect d = -0.09; z-test p = 0.497.
  • 5 mg BI 425809: mean 4.08 versus 4.08 on control; difference 0.00 (95% CI -0.21 to 0.21), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2 mg BI 425809 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 5 mg BI 425809 and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes cover aspects beyond the primary cognitive scale: ADCS-ADL assesses activities of daily living, and CIBIC+ is a clinician’s interview-based impression of change. Across the reported arm-level means, secondary-outcome patterns are mixed rather than consistently aligned across all BI 425809 doses. The reported sponsor analyses are limited to selected contrasts for each outcome; they do not provide a complete model-based comparison for every dose and endpoint in the available record.

At a broad level, the secondary results do not provide a clear, consistent pattern that changes the interpretation of the primary endpoint. They offer additional descriptive context, but they should not be used to turn an uncertain primary finding into a definitive conclusion. These endpoints measure different constructs and have their own variability, missing assessment patterns and analysis choices.

Unadjusted secondary comparisons carry less inferential weight when several outcomes, doses or analyses are considered. The chance of seeing apparently notable results can increase across multiple tests unless the analysis plan controls that multiplicity. The registry record reports 18 analyses overall, but does not report the full multiplicity procedure for secondary outcomes or whether all analyses were prespecified. A p-value from an individual secondary comparison should therefore be treated as exploratory unless its role in a multiplicity-controlled analysis is clear.

The record lists two secondary outcomes, despite listing three outcome measures overall. It does not report all endpoint-specific interpretation thresholds or enough detail to establish how differences on these measures should be judged clinically. Accordingly, secondary outcomes can complement the primary result, but cannot independently resolve the uncertainty in the primary comparison.

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

• Change From Baseline in the Alzheimer's Disease Cooperative Study/Activities of Daily Living (ADCS-ADL) Score After 12 Weeks of Treatment
• Clinician's Interview-Based Impression of Change (CIBIC+) Score After 12 Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis used MCPmod in combination with mixed model repeated measures (MMRM). This joins two statistical tasks: examining whether the outcomes across dose groups are consistent with candidate dose-response shapes, and modelling repeated outcome measurements over visits. The posted record describes the methods but does not report a full statistical analysis plan or every implementation detail.

What does dose-response modelling assess?

Dose-response methods ask whether the outcome pattern across dose levels is compatible with a specified curve or trend. MCPmod considers several candidate shapes rather than relying on a single assumed form. The registry lists Beta, Emax, Sigmoidal Emax, linear, linear in log and logistic model fits. A model-fit p-value assesses compatibility with the tested dose-response structure under the analysis; it is not a direct estimate of the difference between one dose and placebo. The reported values should therefore be read alongside the arm-level estimates and the sponsor’s pairwise model results, not as dose-specific treatment effects.

Considering multiple candidate shapes can reduce reliance on an arbitrary choice of one curve, but it also means the interpretation depends on how the candidates and comparisons are handled. The registry record does not report the full multiplicity procedure, selection rule or decision threshold for the MCPmod results. It identifies the method as MCPmod, but additional procedural details are not reported in the registry record.

Why use a repeated-measures model?

MMRM is a general approach for analysing repeated measurements from the same participant. Rather than reducing the data to one summary change before modelling, it can use the pattern of observed scores across visits and account for the fact that measurements from one person are related. The registry’s primary model included fixed categorical covariates for treatment, visit, baseline MMSE category (>=20, <20 as represented in the record) and treatment-by-visit interaction. It also included continuous fixed covariates for baseline and baseline-by-visit interaction, with patient as a random effect.

The model used an unstructured covariance structure for within-patient measurements. In general, a covariance structure describes how repeated observations relate to one another; an unstructured choice does not impose a simple pattern of equal or steadily changing correlations. This can offer flexibility, while also requiring the observed data to support estimation of the relationships. No additional numerical interpretation of that structure is reported in the registry record.

The same MMRM model used for the primary analysis was also used for the secondary analysis of the primary endpoint. That detail does not mean the simple recalculations of arm-level change means use MMRM: those are unadjusted comparisons reconstructed from posted summary statistics. Nor does it mean all sponsor-reported comparisons use the same summary measure. The registry reports mean differences for some final-value contrasts and median differences for others.

What do the recalculations add?

The unadjusted recalculations compare each dose-group mean change with the placebo mean change. Their confidence intervals use the posted arm-level means and standard deviations, and their p-values are unadjusted. They provide a transparent summary-scale comparison, but they do not account for the repeated-measures modelling or the full covariate structure of the sponsor analysis. A pooled standard deviation is used for the standardized effect description; it characterizes the observed difference relative to variability and is not itself evidence that the difference is important.

These simple comparisons also do not replace the planned MCPmod/MMRM approach. Differences can arise because the analyses use different outcome summaries, modelling assumptions, covariate adjustment and repeated observations. The primary sponsor analysis is the appropriate reference for the trial’s prespecified inferential approach; the recalculations are supplementary context. The registry record does not report an analysis-discrepancy flag, and the listed recalculations are not identified as conflicting with the sponsor’s results.

Why does over-dispersion matter in general?

Over-dispersion is a general concern when observed variation exceeds what a model’s assumed distribution allows. If it is ignored, standard errors can be too small and intervals too narrow. The primary endpoint is treated as a continuous score and analysed with MMRM, not a count model described as requiring a dispersion adjustment. The registry record does not report a specific over-dispersion assessment, so no claim about its presence or absence in this study is warranted.

11. Confidence Intervals and Precision

A confidence interval describes a range of estimates compatible with the observed data and the assumptions of the analysis. It is not a guarantee that the true effect lies within the particular interval, and its width reflects uncertainty as well as the scale of the outcome. For a difference in change, zero represents no difference between the compared group means on that measure.

For the simple unadjusted primary comparisons, all four 95% confidence intervals include zero. The interval for 2 mg versus placebo runs from -1.355 to 1.131; for 5 mg, from -1.161 to 1.235; for 10 mg, from -0.616 to 1.738; and for 25 mg, from -1.462 to 0.838. Because the intervals extend to both sides of zero, these summaries are compatible with differences favoring either group. They do not isolate a precise nonzero difference.

The intervals also differ in their ranges, so precision is not identical across contrasts. Their interpretation is limited to the unadjusted recalculations from arm-level means and standard deviations. The sponsor’s model-based final-value results are separate: the reported 2 mg mean difference was 0.05 with a 95% interval from -1.09 to 1.18, and the 10 mg mean difference was 0.76 with an interval from -0.38 to 1.90. The sponsor reported median differences for 5 mg and 25 mg, so those estimates should not be treated as mean differences.

Statistical uncertainty is not the only limitation on interpretation. The registry record does not report a threshold for a clinically important ADAS-Cog11 difference. Thus, even a narrow interval would need clinical context to judge importance, while an interval that includes zero does not prove exact equivalence. The posted results are best read as showing uncertainty around small estimated differences rather than establishing a precise treatment effect.

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 justification. For these continuous outcomes, the displayed values are participants per arm, rather than total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s original sample-size assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm that, under those assumptions, would give an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column gives the corresponding planning figure for a 90% chance. These are prospective design concepts: they are not the probability that the observed study result is correct, and they do not measure the probability that a treatment effect exists.

The rows labelled 100%, 75% and 50% of the observed effect use progressively smaller effects as the target. Smaller effects are harder to distinguish from random variation and therefore require more participants under the same assumptions. When an observed difference is very close to zero, planning directly from it can produce extremely large figures, as seen for several comparisons. Such figures are sensitive to the observed estimate and should not be interpreted as a recommended sample size without a scientifically justified target effect and design.

These figures are planning illustrations, not observed power. Observed power calculated from the effect estimate after a study is complete adds little beyond the estimate and its confidence interval. The confidence intervals convey the uncertainty in the posted comparisons more directly. The planning assumptions describe the illustration only; the registry record does not report that they were the assumptions used to design this trial.

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 = -0.112; pooled standard deviation σ = 4.901.
2. n = 2 × (1.96 + 0.842)² × 4.901² / -0.112² = 30,060.8, rounded up to 30,061 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 <- -0.112                      # observed difference in means
sigma <- 4.90116875624735                     # 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(2788513)
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 = 30,061 (80% power), 40,243 (90% power)
 75% of observed effect: n per arm = 53,442 (80% power), 71,543 (90% power)
 50% of observed effect: n per arm = 120,244 (80% power), 160,972 (90% power)
power.t.test: 30061.8 
Simulated power at n = 30,061 per arm: 0.800 (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 sponsor’s reported analyses and the unadjusted recalculations answer related but not identical questions. The primary analysis is described as MCPmod combined with MMRM, with treatment, visit, baseline MMSE category, treatment-by-visit interaction, baseline and baseline-by-visit terms, and patient as a random effect. The registry also reports MMRM comparisons of final values. Those model-based results are the sponsor’s analyses and should be distinguished from the simple comparisons reconstructed from posted arm-level change means and standard deviations.

The recalculations compare mean change from baseline for each dose group with the placebo mean. They do not apply the sponsor’s repeated-measures model or its covariate adjustments. Their confidence intervals and unadjusted p-values are useful for understanding the scale and uncertainty of the arm-level summaries, but they are not substitutes for the sponsor’s analysis. In addition, some sponsor-reported final-value comparisons are medians, while others are means. A median contrast is not directly comparable to a mean-change contrast.

The registry reports no discrepancy between the sponsor analysis and the recalculated summaries. The two sets of results are broadly consistent in not establishing a clear separation from placebo, but their estimates and p-values should not be compared as if they were generated by the same analysis. Where a discrepancy between a sponsor analysis and a recalculation is present, the sponsor’s own analysis takes precedence; no such discrepancy is flagged in this record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis makes several statistical comparisons or tests several candidate hypotheses. This study has multiple dose groups, a placebo comparator, multiple candidate dose-response models and secondary outcomes. If many tests are examined, some results may appear notable by chance even when no underlying difference exists. A prespecified multiplicity strategy can help control how strongly the results are interpreted across those tests.

The registry identifies MCPmod for the primary analysis and lists six candidate model fits. That indicates dose-response modelling was part of the approach, but the registry record does not report the full multiplicity adjustment, model-selection rule or exact decision procedure. The reported model-fit p-values should not be interpreted as if they were six independent dose-versus-placebo tests, nor should an unadjusted recalculated p-value be mistaken for a multiplicity-adjusted primary result.

The registry reports 18 analyses, but does not fully describe which comparisons were confirmatory, how secondary endpoints were handled across multiple tests, or whether any analyses were exploratory. These details are important because the evidential meaning of an isolated p-value depends on the testing context. The unadjusted recalculations are especially limited for inference across multiple doses because they do not apply a reported family-wise or other multiplicity correction.

The efficacy population was the full analysis set: randomized patients who received at least one dose and had a baseline plus at least one corresponding post-baseline on-treatment efficacy assessment for an endpoint. This is the population definition reported for efficacy analyses. It is not the same as all enrolled or all randomized patients, and the analysis population may vary by endpoint according to available assessments.

MMRM can use observed repeated measurements, but the record does not report the assumptions used to address missing outcome data, sensitivity analyses for departures from those assumptions, or detailed missingness by group. It is therefore not possible from the registry record to determine how robust the findings are to alternative missing-data assumptions. Interim analyses are not reported in the registry record. The original sample-size justification and complete statistical analysis plan are also not reported in the registry record.

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: fall (1.6%), glaucoma (0.8%), drug-induced liver injury (0.8%), bronchitis (0.8%), hypoglycaemia (0.8%).

The registry record reports serious adverse events for each group using the number at risk and the number affected. The serious-event counts were 5 in the 2 mg group, 4 in the 5 mg group, 4 in the 10 mg group, 4 in the 25 mg group and 5 in the placebo group. The corresponding numbers at risk were 123, 122, 122, 123 and 120. No deaths were reported in any group.

These are descriptive counts during the trial record, not adjusted comparisons of risk. They do not establish whether an event was caused by treatment, and the registry summary does not provide event timing, duration, recurrence or individual clinical context. A count should be read with its group denominator and the study’s duration in mind; it should not be compared as if the groups were identical in every respect.

The record also gives the most frequent serious-event terms, including Fall at 1.6%, and Glaucoma, Drug-induced liver injury, Bronchitis, Hypoglycaemia and Dementia at 0.8% each. These entries describe reported terms and percentages in the registry record. The record’s event summary does not support conclusions about comparative safety beyond these reported counts and terms.

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

The registry results describe a randomized, double-blind comparison of four BI 425809 doses with placebo over a 12-week treatment period in patients with cognitive impairment due to Alzheimer’s disease. On the primary ADAS-Cog11 change outcome, arm means varied across doses, but the simple dose-versus-placebo estimates were small relative to their uncertainty. Every unadjusted 95% confidence interval includes zero, and the posted MCPmod model-fit p-values do not indicate a clear dose-response pattern in this record.

This does not establish that all dose effects are exactly zero. A confidence interval that crosses zero leaves uncertainty about the direction and size of the contrast. Nor does it establish that a potentially important effect was excluded: the record does not report a clinically important difference threshold, and the intervals retain a range of possible differences. The sponsor’s model-based analysis is also distinct from the simple recalculation and should be read according to its repeated-measures and dose-response methods.

Statistical evidence is not the same as clinical importance. The ADAS-Cog11 measures specified cognitive domains, while the secondary outcomes address daily activities and clinician impression. Results across measures can complement one another but do not automatically combine into a single conclusion. The registry record does not report enough detail to assign a clinical meaning threshold to the observed changes or to fully assess missing-data sensitivity.

Safety counts are also descriptive. The reported serious-event counts were similar in scale across the listed groups and no deaths were reported, but the summary does not establish causality or rule out uncommon or longer-term risks. The record pertains to a phase 2 study and a 12-week treatment period. Its results should be understood within that population, outcome set, duration and analysis record, not generalized beyond them.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares several dose levels with placebo and records both a primary cognitive outcome and secondary outcomes addressing daily function and clinician impression. A multi-dose design can examine whether the outcome follows a dose-response pattern, rather than limiting the question to a single active dose. The registry’s use of MCPmod reflects that structure by listing several candidate response shapes.

The results also illustrate why point estimates alone are not enough. The dose-group means move in different directions, but each simple comparison with placebo is uncertain, and all four unadjusted confidence intervals include zero. Reading the estimates alongside their intervals prevents over-interpreting a single arm mean or a model-fit p-value. The sponsor’s MMRM analysis further illustrates how a planned model can account for repeated measurements and baseline characteristics, while simple recalculations from summaries remain supplemental.

Planning illustrations based on observed effects show how strongly proposed sample sizes depend on the effect targeted. When the estimated difference is close to zero, calculations based on that estimate can produce very large participant requirements. That is a property of the illustration, not evidence that a particular future study must use those numbers. A credible design needs a justified target effect and explicit assumptions, which are not reported for the original trial in the registry record.

Finally, the record demonstrates the importance of distinguishing registry summaries from a complete analysis report. It identifies the methods and some model-based results, but does not report all multiplicity, missing-data or design details. Statistical interpretation is strongest when the estimate, uncertainty, model, population and limits of the record are considered together.

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.

The registry record leaves several trial-specific details unreported. It does not give the original sample-size justification, full protocol assumptions, detailed statistical analysis plan, interim-analysis plan or the complete multiplicity procedure. These omissions limit assessment of whether the reported analyses align with all prespecified decisions and how much confirmatory weight to give individual comparisons.

The primary endpoint is measured over the stated 12-week period, with day 1 and day 85 identified as baseline and end-of-trial assessments. The record does not provide longer-term follow-up results. The available duration therefore cannot address persistence of outcomes beyond the treatment period. The registry record also does not report a threshold for a clinically important ADAS-Cog11 change, limiting interpretation of whether a numerical difference would matter to patients or clinicians.

The primary analysis description includes MMRM and an unstructured covariance structure, but the record does not detail sensitivity analyses for missing data or assumptions about missingness. The efficacy population requires a post-baseline on-treatment assessment, so participants without qualifying assessments are not included in that endpoint population. Endpoint-level numbers vary, and the record does not provide enough detail to assess the reasons for missing assessments or their possible influence on results.

Some sponsor-reported comparisons are means and others are medians, while the simple recalculations use mean changes. These are different summaries and should not be merged as though directly interchangeable. The posted secondary analyses are incomplete relative to the full set of dose groups and outcomes, and unadjusted comparisons may be affected by multiplicity. Safety summaries provide counts and selected event terms but not detailed timing, duration, attribution or individual case information.

These limitations do not invalidate the posted results, but they define what can be concluded from the registry record alone. A fuller appraisal would require the complete protocol, analysis plan and study report.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BI 425809 in Patients With Cognitive Impairment Due to Alzheimer's Disease. — NCT02788513.
• Registry record last updated 2020-11-06; status last verified 2020-10.
• Results first posted 2020-11-06.
• 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

NCT02788513 was a completed phase 2, randomized, double-blind, parallel-group study of BI 425809 in patients with cognitive impairment due to Alzheimer’s disease. The registry lists 611 participants enrolled and a 12-week treatment period. Four BI 425809 dose groups were compared with placebo.

The primary outcome was change from baseline in ADAS-Cog11 total score. The registry describes MCPmod with MMRM for the primary analysis and reports six candidate model-fit results. Unadjusted recalculations of dose-versus-placebo mean changes have confidence intervals that include zero. The posted secondary outcomes were ADCS-ADL and CIBIC+.

The record reports serious adverse-event counts by group and no deaths. It does not report the original sample-size justification, a full multiplicity procedure, or detailed missing-data sensitivity analyses. The posted results provide a record of the comparisons and their uncertainty, but do not establish a clear primary-outcome separation from placebo.