BI 409306 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 409306 in Patients With Cognitive Impairment Due to Alzheimer's Disease. (NCT02337907), a randomized phase 2 study. The primary outcome is Change From Baseline in Neuropsychological Test Battery in Total Z-score After 12-week Treatment..

2. Clinical Question

This is a question about a measured cognitive test outcome over the treatment period, not a direct measure of every aspect of daily functioning or disease course. The study also recorded secondary outcomes involving activities of daily living, clinical dementia rating, and another cognitive scale. Those measures provide related but distinct perspectives; their results should not be treated as interchangeable with the primary outcome.

3. Trial Design

The registry describes a phase 2, randomized, double-blind, parallel-group study sponsored by Boehringer Ingelheim. Its official title describes a multicentre comparison of orally administered BI 409306 with placebo during a 12-week treatment period. The registry lists an enrollment of 329 and a completed status. The recorded start date is 2015-01-21, and the primary completion date is 2017-09-15.

The active BI 409306 regimens were 10 mg once daily, 25 mg once daily, 50 mg once daily, and 25 mg twice daily. Placebo matching BI 409306 served as the comparator in the primary-outcome analyses. Donepezil was also listed as an active comparator. The primary outcome data include a pooled BI 409306 group in addition to the individual dose groups; the registry record does not explain in the posted results how that pooled group was formed.

Randomization indicates that assignment to study groups was intended to be determined by chance, while double masking indicates that two categories of people involved in the study were kept unaware of treatment assignment. The registry record does not identify those categories in the information available for this analysis. A parallel-group design compares groups over the same general treatment period rather than switching each participant between treatments.

For the primary outcome, the reported analysis used a full analysis set defined by treatment exposure and availability of baseline and post-baseline assessment. The outcome summaries identify observed cases. The registry record does not report the original sample-size justification, the planned allocation ratio, or further details of the protocol. Enrollment should not be confused with the analysis population for each outcome: the analysis counts shown for particular outcomes can differ from the overall enrollment.

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: All patients were screened for eligibility. All patients eligible after screening underwent a 2-week single-blind placebo run-in period before randomisation. Patients were not to be randomized to trial treatment if any one of the specific entry criteria were not met.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS): FAS includes all randomised patients who were treated with at least one dose of trial medication and had a baseline and at least one post-baseline on-treatment primary endpoint NTB or secondary endpoint assessment. Observed cases (OC)

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) included all patients who were randomised and treated with at least one dose of trial medication.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Neuropsychological Test Battery in Total Z-score After 12-week Treatment., measured over Baseline and 12 weeks.

The primary endpoint is change from baseline in total z-score on the Neuropsychological Test Battery after 12 weeks of treatment. The battery consists of 9 validated components. The registry describes converting each component's raw score to a z-score using the baseline mean and standard deviation for that test, then averaging the resulting scores to form the total z-score.

A z-score expresses a value in standard-deviation units relative to the baseline reference used for that test. In the registry's description, 0 represents the baseline mean; positive values are higher than baseline and negative values are lower than baseline. The endpoint therefore combines performance across the battery rather than reporting each component as a separate primary outcome.

Change in a standardized composite can be useful when the clinical question concerns a broad cognitive measure assembled from several tests. It places the component scores on a common standardized scale before averaging them, although the total score does not show whether every component changed in the same way. The registry describes the reported least-squares mean as an adjusted mean change from baseline. The primary endpoint is thus a model-based summary of average change, not a count of participants who improved or worsened.

The endpoint is measured at baseline and 12 weeks. It captures the study's designated short-term cognitive outcome during the treatment period. The registry record does not report a threshold for a clinically important difference on this measure, so the statistical estimates alone do not establish how large a change would be meaningful to patients.

7. Results Posted in the Registry

• BI 409306 10 Milligram (mg) Once Daily (QD): mean 0.13 versus 0.15 on control; difference -0.02 (95% CI -0.17 to 0.13), standardized effect d = -0.04; z-test p = 0.788.
• BI 409306 25 mg QD: mean 0.17 versus 0.15 on control; difference 0.02 (95% CI -0.13 to 0.17), standardized effect d = 0.04; z-test p = 0.792.
• BI 409306 50 mg QD: mean 0.16 versus 0.15 on control; difference 0.01 (95% CI -0.13 to 0.15), standardized effect d = 0.02; z-test p = 0.889.
• BI 409306 25 mg Twice Daily (BID): mean 0.01 versus 0.15 on control; difference -0.14 (95% CI -0.29 to 0.01), standardized effect d = -0.31; z-test p = 0.062.

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 Alzheimer's Disease Cooperative Study/Activities of Daily Living (ADCS-ADL) Total Score After 12-week 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 errors.
• Result:
  • BI 409306 10 Milligram (mg) Once Daily (QD): mean 0.10 versus -0.58 on control; difference 0.68 (95% CI -1.41 to 2.77), standardized effect d = 0.11; z-test p = 0.523.
  • BI 409306 25 mg QD: mean -0.99 versus -0.58 on control; difference -0.41 (95% CI -2.56 to 1.74), standardized effect d = -0.06; z-test p = 0.709.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 409306 10 Milligram (mg) Once Daily (QD) 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 BI 409306 25 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Clinical Dementia Rating Scale Sum of Boxes (CDR-SB) Total Score After 12-week 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 errors.
• Result:
  • BI 409306 10 Milligram (mg) Once Daily (QD): mean 0.10 versus 0.10 on control; difference 0.00 (95% CI -0.55 to 0.55), standardized effect d = 0.00; z-test p = 1.000.
  • BI 409306 25 mg QD: mean 0.30 versus 0.10 on control; difference 0.20 (95% CI -0.35 to 0.75), standardized effect d = 0.12; z-test p = 0.475.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 409306 10 Milligram (mg) Once Daily (QD) 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 BI 409306 25 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Alzheimer's Disease Assessment Scale-cognitive Subscale (ADAS-cog11) Total Score After 12-week 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 errors.
• Result:
  • BI 409306 10 Milligram (mg) Once Daily (QD): mean 1.14 versus -0.18 on control; difference 1.32 (95% CI -0.51 to 3.15), standardized effect d = 0.24; z-test p = 0.156.
  • BI 409306 25 mg QD: mean 0.94 versus -0.18 on control; difference 1.12 (95% CI -0.76 to 3.00), standardized effect d = 0.20; z-test p = 0.244.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 409306 10 Milligram (mg) Once Daily (QD) 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 BI 409306 25 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover activities of daily living, clinical dementia rating, and cognitive performance on the ADAS-cog11 scale. Across these different measures, the dose-level estimates do not form a consistent pattern that would clearly reinforce a treatment separation on the primary outcome. This broad pattern is more informative than treating any isolated estimate as decisive, especially given the uncertainty in the reported comparisons.

The secondary outcomes are related to the primary cognitive measure, but they assess different constructs and use different scales. Their estimates therefore cannot be compared by simply treating a larger numerical value on one scale as a larger effect on another. The registry record does not report thresholds for clinically important changes for these secondary measures.

For the secondary outcomes, sponsor analyses are posted for selected comparisons, rather than for every dose and every secondary measure. Where analyses are posted, the reported confidence intervals include values on both sides of zero. Results for unreported comparisons are not reported in the registry record and should not be inferred from the displayed group summaries.

Secondary outcomes can help assess whether a pattern is coherent across related measures, but their evidential weight depends on how they were prespecified and analyzed. The registry record does not report a multiplicity adjustment or a testing hierarchy for these secondary results. When multiple outcomes and dose comparisons are examined, unadjusted results have a greater chance of producing apparently notable findings by chance. These findings should therefore be considered supportive and exploratory rather than as independent confirmation of the primary result.

Overall, the secondary findings do not remove the uncertainty in the primary-outcome comparison. They broaden the descriptive picture, but they do not establish a consistent, definitive difference between BI 409306 and placebo.

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

• Change From Baseline in Alzheimer's Disease Cooperative Study/Activities of Daily Living (ADCS-ADL) Total Score After 12-week Treatment
• Change From Baseline in Clinical Dementia Rating Scale Sum of Boxes (CDR-SB) Total Score After 12-week Treatment
• Change From Baseline in Alzheimer's Disease Assessment Scale-cognitive Subscale (ADAS-cog11) Total Score After 12-week Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports least-squares means for the primary endpoint. In general, a least-squares mean is a model-based estimate of an average that accounts for terms included in the statistical model; it can differ from a simple arithmetic average. The registry specifically describes the primary least-squares mean as an adjusted mean change from baseline. The details of every adjustment term are not reported in the registry record.

What does a repeated-measures model do?

The sponsor used a mixed model for repeated measurement for the primary outcome. In general, repeated-measures models analyze measurements taken at multiple times while recognizing that measurements from the same participant are related. They can use information across visits to estimate group differences over time and can accommodate some incomplete measurement patterns under model assumptions. The registry record does not report the full model specification, its covariance structure, or the assumptions used for handling missing outcomes. The fact that a model can use repeated observations does not guarantee that missingness is harmless or that its assumptions hold.

The registry identifies the analysis population as the full analysis set. This set includes randomized participants who received at least one dose of trial medication and had a baseline and at least one post-baseline, on-treatment primary or secondary endpoint assessment. The primary results are also described as observed cases. These definitions matter: the reported estimates do not necessarily represent every randomized participant or every enrolled participant. The registry record does not provide further detail about participant flow or the number of missing endpoint observations in the information used for this analysis.

How should the recalculated comparisons be read?

The recalculated comparisons use the posted group means and standard errors to approximate unadjusted mean differences and their uncertainty. This is not the same procedure as refitting the sponsor's repeated-measures model. The pooled standard deviations used in those approximations are marked as approximate, and the recalculated intervals should therefore be regarded as illustrations based on group summaries rather than as a reconstruction of the trial's full analysis.

For the four dose-specific primary comparisons, the unadjusted recalculations and the sponsor's estimates are broadly similar in direction and magnitude. Small differences are expected because the approaches differ. For the pooled comparison, however, the recalculated uncertainty is notably different from the sponsor-reported uncertainty. This discrepancy is a reason not to substitute the summary-statistic calculation for the sponsor's model-based result. The sponsor's own analysis takes precedence.

What does the p-value test?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis, under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor's analyses are reported as superiority tests. The posted results do not report multiplicity-adjusted p-values, and the registry record does not state a familywise testing strategy for the several dose comparisons.

The recalculated p-values are unadjusted tests based on approximate summary-statistic calculations. They are not a replacement for the sponsor's model-based tests and do not account for any adjustment or modeling detail that may be part of the sponsor analysis. In reading results, the estimate and interval are more informative about direction and precision than a threshold judgment based on a p-value alone.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model or simple calculation expects. A larger standard deviation increases uncertainty around a group comparison and can widen its interval. The pooled primary-outcome group has a reported standard error that is markedly larger than the dose-specific standard errors, and its summary-statistic recalculation consequently yields a very large approximate pooled standard deviation. The registry record does not explain this difference. It reinforces the need to interpret that recalculation cautiously rather than infer an underlying cause.

The trial's formal analysis plan, original sample-size assumptions, interim-analysis arrangements, and detailed missing-data strategy are not reported in the registry record. General explanations of the statistical methods do not fill those gaps or establish which assumptions the study team prespecified.

11. Confidence Intervals and Precision

A confidence interval describes a range of estimates compatible with the observed data under the analysis method and its assumptions. It conveys uncertainty around the estimated mean difference; it is not a range containing a specified proportion of individual participants' outcomes. A narrower interval indicates greater statistical precision, while a wider interval indicates less precision.

The sponsor-reported primary intervals for the dose-specific comparisons include zero. This means the data are compatible with no mean difference as well as with differences in either direction covered by the respective interval. For example, the reported interval for 10 mg once daily extends from -0.163 to 0.124, and the interval for 25 mg once daily extends from -0.125 to 0.171. The reported intervals for 50 mg once daily and 25 mg twice daily also span zero. The pooled sponsor-reported interval runs from -0.135 to 0.074.

The intervals are not so narrow that they establish near-identical outcomes. Their breadth leaves room for differences that could matter statistically, but the registry record does not give a threshold for clinical importance on the z-score scale. The point estimate alone cannot resolve that uncertainty. The interval also does not account for every possible limitation, such as model misspecification, missing-data assumptions, or multiple comparisons.

The recalculated intervals come from unadjusted approximations based on posted summaries, not the sponsor's repeated-measures model. The pooled recalculated interval is especially different from the sponsor's result, so it should not be used to characterize the official pooled estimate's precision. The sponsor's reported interval is the appropriate reference for the trial's own analysis, while the recalculation is best treated as a check that highlights how assumptions and methods can affect uncertainty.

Confidence intervals and p-values answer related but distinct questions. An interval makes the range of plausible effect estimates more visible; a p-value summarizes compatibility with a null hypothesis under the test. Neither alone establishes clinical importance or proves absence of an 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 sample-size illustrations express the required number of participants per arm for these continuous-outcome comparisons. They do not give a total across arms or total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The original trial's own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes an illustrative design that, under the stated assumptions and if the assumed effect were real, would have an 80% chance of producing a statistically significant result. The 90% power column represents a higher target chance under the same assumptions. These are prospective planning calculations, not observed power for the completed trial. Observed power is not a useful substitute for interpreting the estimates and confidence intervals from the actual data.

Rows planning for 100%, 75%, and 50% of the observed effect show how changing the assumed effect changes the planning requirement. Smaller effects need more participants to detect, all else equal. If the observed effect is close to zero, calculations based on a fraction of that estimate can become extremely large or unstable; the table is therefore an illustration of the selected effect assumptions, not a recommendation or a design conclusion.

The plotted curve should be read as a visual version of the same planning relationship: the required participants per arm vary with the target effect under the stated assumptions. It does not show observed participant outcomes or the probability that the treatment works. These calculations do not replace the sponsor's design planning, which is not described in the registry record.

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 = -0.020; pooled standard deviation σ = 0.446.
2. n = 2 × (1.96 + 0.842)² × 0.446² / -0.020² = 7,801.5, rounded up to 7,802 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 <- -0.02                      # observed difference in means
sigma <- 0.445860569078298                     # 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(2337907)
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 = 7,802 (80% power), 10,444 (90% power)
 75% of observed effect: n per arm = 13,870 (80% power), 18,568 (90% power)
 50% of observed effect: n per arm = 31,206 (80% power), 41,776 (90% power)
power.t.test: 7802.4 
Simulated power at n = 7,802 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 sponsor's own primary analyses used a mixed model for repeated measurement and reported adjusted comparisons with 95% confidence intervals. The summary-statistic recalculations are simple unadjusted approximations. They use the posted means and standard errors, and do not reproduce the repeated-measures model or its adjustments.

For the dose-specific comparisons, recalculated estimates and sponsor estimates are generally close, though the estimates, intervals, and p-values are not identical. This is expected when analyses differ in modeling and adjustment. The recalculated intervals are not substitutes for the reported analyses.

The pooled comparison has a more pronounced discrepancy: the recalculated interval is far wider than the sponsor's reported interval. The registry record does not explain why the summary statistics produce that difference. Because the discrepancy is flagged, the sponsor's own analysis takes precedence for interpreting the trial's reported result. The recalculation remains useful as a caution about what can happen when adjusted longitudinal results are approximated from group summaries, but it should not be treated as an alternative official finding.

The sponsor's results do not show a clear superiority difference from placebo on the primary endpoint. That interpretation rests on the reported estimates and intervals, not on a claim that the recalculated methods validate the sponsor's model.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes several BI 409306 dose comparisons, a pooled comparison, and multiple secondary outcomes. Testing many comparisons can increase the chance of at least one apparently positive result even when there is no true difference across the set. Statistical approaches such as a prespecified testing hierarchy or multiplicity adjustment can address that issue, but the registry record does not report a planned strategy for controlling multiplicity.

The posted sponsor analyses are labeled as superiority comparisons. The registry record does not report a formal hierarchy that would determine which comparison is primary among the several doses, whether testing of later outcomes depended on earlier results, or whether the reported p-values were adjusted. The primary endpoint remains the designated main outcome, but the absence of a reported multiplicity plan limits interpretation of secondary and additional comparisons.

The primary analysis population is described as the full analysis set: randomized participants treated with at least one dose and with baseline plus at least one post-baseline, on-treatment primary or secondary assessment. The primary data are also described as observed cases. That definition excludes some randomized participants from the analysis if they did not meet those assessment criteria. The registry record does not report a detailed accounting of missing measurements, reasons for missingness, or how missing values were handled in the model.

In general, repeated-measures models can use available observations without filling in every missing value, but their estimates rely on assumptions about the observation process and the model. The registry record does not specify the sponsor's assumptions or report sensitivity analyses for departures from them. It also does not report whether any interim analyses were planned or conducted, or provide a fuller statistical analysis plan. These details should not be guessed from the posted outcome results.

Accordingly, the primary comparison can be interpreted as reported, while the evidence from multiple secondary and dose-specific tests warrants caution. The missing multiplicity and missing-data details do not invalidate the posted results, but they limit how confidently the full set of comparisons can be interpreted as confirmatory.

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: suicidal ideation (3.6%), angina pectoris (1.9%), cerebrovascular accident (1.9%), delirium (1.9%), vertigo positional (1.8%).

The registry reports serious adverse events, other adverse events, and deaths by listed safety group. Serious adverse events were reported for 1 of 55 participants in the 10 mg once-daily group, 3 of 53 in the 25 mg once-daily group, 1 of 55 in the 50 mg once-daily group, and 3 of 55 in the 25 mg twice-daily group. The matching-placebo group had 8 of 106 participants with a serious adverse event. The Donepezil QD group had 0 of 5.

Other adverse events were reported for 6 of 55, 9 of 53, 7 of 55, and 2 of 55 participants across the four BI 409306 dose groups, respectively. The matching-placebo group had 8 of 106, and the Donepezil QD group had 1 of 5. One death was reported in the 10 mg once-daily group; no deaths were reported in the other listed groups.

These counts describe events recorded in the registry and do not establish that treatment caused them. The safety groups and outcome-analysis groups have different denominators, and the Donepezil group is small. The registry lists suicidal ideation as a serious-event term at 3.6%, with angina pectoris and cerebrovascular accident at 1.9% each. The record does not provide the context needed to attribute these terms to a particular treatment from those overall percentages alone.

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

The posted results describe average changes on a standardized cognitive test over a 12-week treatment period. The sponsor's reported comparisons do not establish a clear difference between the studied BI 409306 regimens and placebo on that primary measure. Their confidence intervals include zero, and the estimates leave uncertainty about the magnitude and direction of any group differences.

This conclusion is limited to the outcomes, population, and treatment period recorded in the registry. It does not show that every participant had the average outcome, and it does not determine whether an individual participant experienced a meaningful change. The total z-score averages results across 9 tests, so a group-level composite does not reveal the pattern for each component test.

A non-significant superiority result is not proof of equivalence, and it does not establish that the treatments have identical effects. The registry record does not report an equivalence margin or an equivalence design. Nor does an estimate that is numerically positive or negative establish clinical importance; the record does not give a threshold for meaningful change on the primary z-score scale.

The secondary measures offer additional information about daily function and other cognitive or clinical rating outcomes, but they do not create a consistent, decisive pattern that resolves the primary uncertainty. Multiple unadjusted comparisons also make isolated secondary findings less persuasive. Safety counts are descriptive and cannot by themselves establish causation or comparative safety.

The appropriate reading is therefore restrained: the trial's reported primary analyses do not demonstrate a clear superiority difference from placebo, while the uncertainty in the estimates means they also do not demonstrate that no difference exists. These findings are not medical advice and do not determine treatment decisions.

18. Why This Trial Matters Statistically

This trial illustrates why a reported group estimate should be read together with its confidence interval and analysis method. A point estimate can suggest a direction, but the interval indicates how much uncertainty surrounds that estimate. In the primary comparisons, intervals extending across zero prevent a confident conclusion about the direction of the average difference.

It also illustrates the distinction between an adjusted longitudinal analysis and a simple calculation from summary statistics. The sponsor used a repeated-measures model, while recalculations from posted means and standard errors are unadjusted approximations. Their difference is particularly marked for the pooled comparison. Statistical results cannot be detached from the method that produced them, and a convenient reanalysis does not automatically supersede the trial's reported model.

The multiple dose groups and secondary outcomes make multiplicity relevant. A set of unadjusted tests should not be read as if each were the only comparison planned. Without a reported hierarchy or adjustment, secondary findings are less secure as confirmatory evidence. The registry record's limited reporting of multiplicity and missing-data methods is itself important context for evaluating the strength of claims.

Finally, sample-size illustrations based on observed effects are not evidence of the trial's original design assumptions and are not observed power. They show how strongly planning requirements depend on the effect size selected. This makes clear why planning assumptions should be prespecified and reported, and why a completed study's estimate and interval are more useful than a retrospective power calculation for interpreting its result.

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 does not report the original sample-size justification, the study's planned allocation ratio, or enough detail to assess how the study was designed to detect a target difference. The planning illustrations based on observed effects are not a substitute for those original design details.

The primary results use an analysis population requiring treatment exposure and post-baseline assessment, and are described as observed cases. Detailed participant flow, missing outcome counts, reasons for missing assessments, and sensitivity analyses are not reported in the registry record. The repeated-measures model's full specification and missing-data assumptions are also not reported.

There are several dose comparisons and secondary outcomes, but the registry record does not report a multiplicity strategy or a testing hierarchy. This limits the strength of interpretation across the full set of comparisons. Sponsor analyses for the secondary outcomes are posted for selected groups and measures; other analyses are not reported in the registry record.

A discrepancy is present between the summary-statistic recalculation and the sponsor-reported pooled primary comparison. In particular, the recalculated uncertainty is much wider. The sponsor's model-based analysis takes precedence, but the record does not explain the discrepancy. The listed group summaries also identify observed-case estimates, which may not represent all randomized participants.

The treatment period was 12 weeks, and the primary endpoint is a composite cognitive measure. The registry record does not provide a clinical-importance threshold for the z-score or detailed results for each test component. The safety data are descriptive, including a small Donepezil group, and cannot establish causation from counts alone. These limitations constrain interpretation without negating the posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BI 409306 in Patients With Cognitive Impairment Due to Alzheimer's Disease. — NCT02337907.
• Registry record last updated 2018-11-14; status last verified 2018-10.
• Results first posted 2018-11-14.
• 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

NCT02337907 is a completed phase 2 randomized, double-blind, parallel-group study of BI 409306 in people with cognitive impairment due to Alzheimer's disease. The official title describes oral treatment over 12 weeks compared with placebo. The registry lists an enrollment of 329 and four BI 409306 dose regimens, matching placebo, and Donepezil as an active comparator.

The primary endpoint was change from baseline in Neuropsychological Test Battery total z-score. Sponsor-reported repeated-measures comparisons did not establish a clear difference from placebo. The secondary outcomes address activities of daily living, clinical dementia rating, and cognitive performance. Interpretation is limited by uncertainty in the estimates and by details not reported in the registry record, including the original sample-size justification, multiplicity strategy, and fuller missing-data methods.