Study of Donepezil in Female Breast Cancer Survivors With Cognitive Dysfunction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Donepezil in Female Breast Cancer Survivors With Cognitive Dysfunction (NCT01466270), a randomized phase 2 study. The primary outcome is Retention.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase II study of donepezil hydrochloride and placebo in female breast cancer survivors with self-reported cognitive dysfunction after chemotherapy. The registry lists an enrollment of 62 and records the study as completed. The sponsor was Wake Forest University Health Sciences. The recorded start is 2012-07, and primary completion is recorded as 2013-10-01.

Participants were assigned to one of two groups. Arm I received donepezil hydrochloride by mouth once daily; Arm II received placebo by mouth once daily. The primary outcome lists 31.0 participants in each arm. The study is marked randomized and quadruple-masked. The registry record does not report the allocation-generation method, concealment procedures, or the identities of the groups covered by the masking designation.

The main endpoint was retention at 24 weeks, defined in the registry as the percentage of participants who stayed in the study for that period. The primary population is described as all randomized patients. The posted primary results are mean percentages with standard errors. Two secondary outcomes are also posted: HVLT-IR, measured as number of words recalled, and fatigue, measured in units on a scale. Both secondary outcomes are recorded at 24 weeks and use least-squares means with standard errors.

The registry record does not report the protocol's original sample-size justification, the planned statistical analysis, or whether interim analyses were conducted. It also does not specify the operational details of retention assessment or explain how missing outcome measurements were handled. Those omissions limit what can be inferred about the intended analysis and the relation between the posted summaries and any prespecified plan.

4. Participant Flow and Accounting

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

Before assignment: No wash-out or run-in period. All enrolled patients were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized patients

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 patients.

6. Primary Endpoint

The registry lists the primary outcome as Retention, measured over 24 Weeks.

The primary endpoint is retention, expressed as the percentage of participants who stayed in the study through 24 weeks. The registry specifies all randomized patients as the outcome population and reports a mean for each arm, with a standard error. The endpoint therefore describes continued study participation, not a direct cognitive test score or a measure of symptom improvement.

Retention is useful in a feasibility study because it gives information about whether participants remain engaged through the planned follow-up. In general, a study may use retention to assess the practicality of conducting longer or more extensive research in a similar population. That general role should not be confused with evidence about an intervention's clinical effect: retention can be influenced by many factors, and it does not itself establish a change in cognition, fatigue, or any other health outcome.

The posted mean was 71.0% for Arm I, the donepezil group, and 80.7% for Arm II, the placebo group. The unadjusted mean difference was 9.7 percentage points, with a confidence interval that includes values on either side of no difference. Thus, the observed means place retention higher in the placebo group, while the estimate remains imprecise. These data describe this study's recorded retention outcome; they do not establish why participants stayed or left, nor do they determine what retention might be in another study.

7. Results Posted in the Registry

• Arm II: mean 80.70 versus 71.00 on control; difference 9.70 (95% CI -11.84 to 31.24), standardized effect d = 0.22; z-test p = 0.377.

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.

HVLT-IR

• 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:
  • Arm I - Donepezil: mean 25.58 versus 22.94 on control; difference 2.64 (95% CI -0.97 to 6.25), standardized effect d = 0.37; z-test p = 0.151.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I - Donepezil and the control. The interval gives the range of effects that remain compatible with the data.

Fatigue

• 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:
  • Arm I - Donepezil: mean 35.89 versus 35.51 on control; difference 0.38 (95% CI -5.47 to 6.23), standardized effect d = 0.03; z-test p = 0.899.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I - Donepezil and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes address cognition and fatigue rather than retention. Their numerical comparisons are both positive in the stated donepezil-minus-placebo direction, but the clinical meaning of a positive change depends on how each measure is scored. The registry record does not report enough scale interpretation to assign a beneficial or unfavorable meaning to the fatigue contrast. These outcomes therefore add descriptive context without changing what the primary endpoint measures.

The secondary patterns do not provide a simple confirmation of the primary result. Retention is a feasibility measure, while HVLT-IR and fatigue are outcome measures on different scales. A group contrast in one domain need not move in the same direction or have the same interpretation as a contrast in another. The endpoint types should be kept separate rather than combined into a single overall judgment.

The displayed secondary comparisons are unadjusted. When several outcomes are considered, some apparent differences can arise by chance, even if no underlying effect exists. Adjusting for multiplicity is one general way to account for repeated testing, but no adjustment method is reported in the registry record. Without a reported prespecified hierarchy or multiplicity strategy, the secondary estimates carry less confirmatory weight than a single primary comparison designed to address the main question.

The registry lists four outcome measures but posts two secondary outcomes, and it records no reported analyses for those outcomes. This makes the completeness of the outcome reporting difficult to assess. It is not possible from the registry record to determine whether other outcomes were planned, whether the posted outcomes were selected after examining data, or whether the reported secondary summaries correspond to the original analysis plan. Those uncertainties favor cautious, exploratory interpretation.

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

• HVLT-IR
• Fatigue

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous in the registry's statistical classification because it is summarized as a mean percentage. That classification describes how the posted summary is represented; it does not mean that individual retention is intrinsically a continuous event. The arm-level values are mean retention percentages, accompanied by standard errors. A standard error describes the estimated uncertainty in a group mean, rather than the spread of individual participant outcomes.

What does the mean difference describe?

A mean difference puts two group means on the same measurement scale and subtracts one from the other. For the primary comparison, the recorded estimate is 9.7 percentage points for placebo minus donepezil. The sign depends on the stated comparison order: a positive value means the placebo-group mean is larger. It is an absolute contrast on the percentage scale, not a relative percentage change. No relative contrast is calculated.

The comparison estimate is an unadjusted recalculation from the posted summary statistics. It does not incorporate adjustment for baseline variables or other covariates. The registry record does not report whether an adjusted analysis was prespecified or conducted. No sponsor-analysis discrepancy is recorded, but the record lists no reported analyses, so the recalculation should not be interpreted as a detailed reconstruction of the investigators' analytic workflow.

What does a confidence interval add?

A confidence interval describes uncertainty around an estimate under a statistical procedure and its assumptions. It gives a range of values compatible with the observed data at the stated confidence level; it is not a guarantee that the true value lies in that particular interval. When an interval includes no difference, the data do not sharply distinguish the observed contrast from no group difference under that procedure. A wide interval also communicates limited precision: values substantially different from the point estimate remain compatible with the observations.

The primary interval extends from -11.84 to 31.24. It crosses zero, the value representing no difference, and spans contrasts in both directions. The corresponding unadjusted p-value is 0.377. These summaries are related but answer different questions: the interval describes a range and direction of uncertainty, while the p-value measures how the data compare with a null hypothesis under a statistical model. Neither is a measure of clinical importance.

Why does over-dispersion matter in general?

In general, over-dispersion occurs when the variability in observed data is greater than a model assumes. If a model understates variability, its standard errors can be too small and its intervals too narrow, making results appear more precise than they are. A model that allows appropriate variability can better represent uncertainty. This is a general statistical consideration, not a claim that over-dispersion was assessed or found in this study. The registry record does not report a model-based analysis or an over-dispersion assessment for retention.

The secondary outcomes are recorded as least-squares means, which generally refer to means estimated from a statistical model, often with adjustment for specified factors. However, the registry record does not identify the model, covariates, or estimation method behind those least-squares means. Their posted standard errors and contrasts can be described, but the missing model details prevent a more specific account of how the adjusted estimates were obtained. The simple comparison calculations attached to those outcomes are unadjusted and rely on summary statistics; for those recalculations, the pooled standard deviation is approximate.

How should the secondary comparisons be treated?

The HVLT-IR and fatigue results are secondary, and their posted comparison p-values are unadjusted. When multiple outcomes are examined, the chance of obtaining one or more apparently notable results by chance can increase. In general, multiplicity procedures can control that risk, but the registry record does not report whether any such procedure was planned or applied. These results are consequently best treated as exploratory descriptions rather than as independent, confirmatory tests.

The available summaries do not provide a complete account of missing-data methods, assumptions, or sensitivity analyses. Nor does the record describe whether the outcome models followed an intention-to-treat principle or another analysis population for the secondary outcomes. The primary outcome population is identified as all randomized patients, but that label alone does not establish how unavailable retention measurements were handled. Statistical interpretation should therefore remain anchored to the posted summaries and their stated limitations.

11. Confidence Intervals and Precision

The primary retention estimate is 9.7 percentage points for placebo minus donepezil. Its 95% confidence interval ranges from -11.84 to 31.24. Because the interval crosses zero, the data are compatible with no difference as well as with a contrast in either direction. Its width also signals that the point estimate should not be read as a highly precise description of the underlying group difference.

The arm-level means are 71.0% for donepezil and 80.7% for placebo, with standard errors of 8.3 and 7.2, respectively. A standard error is about the uncertainty in an estimated mean, not a range containing most individuals. The confidence interval for the comparison is more directly useful for judging uncertainty in the contrast between groups. It shows that the estimate does not isolate a narrow range of possible differences.

In general, a confidence interval is constructed by a method that has a stated long-run coverage property when its assumptions hold. It does not mean there is a 95% probability that the fixed true effect lies within the particular interval. The interval also does not tell whether any value within it would be clinically important; that requires a meaningful threshold, which is not reported in the registry record.

The primary outcome has no posted lower or upper confidence limits for each arm, and the registry record does not give further detail about the method used for the comparison interval. The interval should therefore be interpreted as the uncertainty attached to the displayed unadjusted recalculation, rather than as a fully documented model-based result. For the secondary measures, the posted group means and standard errors likewise do not replace the need for the underlying analysis specification.

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 for 80% power and participants per arm for 90% power. They are not total events: the registry's planning assumptions specify participants per arm for non-time-to-event outcomes, as in this study. The illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect.

For retention, the planning illustration lists 313 participants per arm for 80% power and 418 participants per arm for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect lists 556 participants per arm for 80% power and 744 participants per arm for 90% power. Planning for 50% of the observed effect lists 1,249 participants per arm for 80% power and 1,672 participants per arm for 90% power.

In plain language, a power target describes the probability of detecting an effect of the specified size under the planning assumptions if that effect is present. The 90% column aims for a greater chance of detecting that assumed effect than the 80% column, and therefore calls for more participants per arm. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants.

These values are planning illustrations based on the observed effect, not the trial's original design rationale; the original sample-size assumptions are not reported in the registry record. They are not observed power. Because the observed effect may be imprecise and may not represent a stable effect size, the figures should be read as conditional planning examples, not as a forecast or a recommendation for a future study.

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 = 9.700; pooled standard deviation σ = 43.259.
2. n = 2 × (1.96 + 0.842)² × 43.259² / 9.700² = 312.2, rounded up to 313 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 <- 9.7                      # observed difference in means
sigma <- 43.2586985472286                     # 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(1466270)
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 = 313 (80% power), 418 (90% power)
 75% of observed effect: n per arm = 556 (80% power), 744 (90% power)
 50% of observed effect: n per arm = 1,249 (80% power), 1,672 (90% power)
power.t.test: 313.2 
Simulated power at n = 313 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures, while two secondary outcomes are posted in addition to the primary retention outcome. The record does not describe a multiplicity strategy, such as a testing hierarchy or adjustment of significance levels. This matters because repeated statistical testing can increase the chance of at least one apparently unusual result even when the underlying effects are absent. As a general principle, unadjusted secondary p-values should not be treated as if each were the sole prespecified test.

The secondary comparisons are explicitly unadjusted, and no reported analyses are listed for them. The registry record does not state whether the outcomes were selected in advance, whether all planned analyses were reported, or whether any adjustment was performed outside the posted record. It is therefore not possible to determine how strongly the secondary results were protected from multiplicity or how they fit into the original analysis plan.

Missing-data methods are also not reported in the registry record. The primary population is described as all randomized patients, but that designation does not explain how missing retention information was treated, whether all randomized participants contributed to the endpoint summary, or what assumptions were used for unavailable observations. The secondary outcome summaries list 30.0 participants per arm, but the registry does not explain why those analysis counts differ from the primary outcome counts.

The record does not report sensitivity analyses for missing data, analysis-population definitions beyond the primary population label, or a statistical analysis plan. These gaps prevent assessment of whether results are robust to alternative assumptions or whether the posted summaries follow prespecified methods. They are limitations of what can be concluded from the registry record, not evidence that a particular analysis was or was not conducted elsewhere.

15. Safety Results

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

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: insomnia (7.1%), headache (3.6%), muscle cramps (3.3%), pain: chest wall (3.3%).

The registry reports serious adverse events for Arm I - Donepezil and Arm II - Placebo. In the donepezil group, 2 of 28 participants at risk were affected; in the placebo group, 1 of 30 participants at risk was affected. These figures describe the recorded participant counts for serious adverse events, with the stated at-risk denominators. The registry also reports other, non-serious adverse events affecting 28 of 28 participants at risk in the donepezil group and 30 of 30 in the placebo group.

The registry lists insomnia at 7.1%, headache at 3.6%, muscle cramps at 3.3%, and chest wall pain at 3.3% among the top serious-event terms. The record does not provide further context for those terms in the information reported, so they should not be interpreted as arm-specific rates. Death counts are not reported in the registry record.

These counts describe reported events in this study; they do not establish comparative safety or identify the cause of an event. Small observed counts can leave substantial uncertainty, and the registry information does not provide detailed event narratives, timing, duration, or attribution. The figures should therefore be read as a limited summary of recorded adverse events rather than a complete safety assessment.

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

The main result describes retention through 24 weeks in a randomized comparison of donepezil and placebo. The observed mean retention was 71.0% in the donepezil arm and 80.7% in the placebo arm. The unadjusted estimated difference was 9.7 percentage points for placebo minus donepezil, with a 95% confidence interval from -11.84 to 31.24. This interval includes no difference and values in both directions, indicating that the contrast is uncertain.

The result does not demonstrate that one group had reliably higher retention than the other. It also does not establish that the groups were equivalent: showing equivalence requires an appropriate design, a prespecified margin, and analysis directed at that question, none of which is reported in the registry record. A nonsignificant p-value is not proof of no effect, and the confidence interval remains compatible with a range of contrasts.

Retention is not cognitive performance. The primary endpoint indicates whether participants stayed in the study, not whether their cognition improved or worsened. The posted secondary outcomes include a word-recall measure and fatigue, but their existence does not transform the primary result into evidence of a cognitive or symptom effect. Their unadjusted status and the missing analysis details further limit confirmatory interpretation.

The findings should also be kept within the study's recorded population and setting: female breast cancer survivors with self-reported cognitive dysfunction following chemotherapy. The registry record does not report enough information about recruitment, eligibility details, missing data, analysis methods, or the original design rationale to support broader claims. No conclusion about effectiveness, clinical importance, or applicability to other populations follows from retention estimates alone.

17. Why This Trial Matters Statistically

This study illustrates why a feasibility outcome and a clinical outcome answer different statistical questions. Retention can inform whether participants remain through follow-up, while cognitive test scores and fatigue address other aspects of the study. Keeping these outcomes distinct prevents an operational measure from being mistaken for evidence of a clinical change.

It also shows the value of reading an estimate together with its uncertainty. The primary contrast is a single number, but its confidence interval spans zero and includes differences in either direction. A point estimate alone can encourage an overly definite interpretation; the interval makes clear that the data leave considerable uncertainty about the size and direction of the retention contrast.

The trial is a useful example of the limits of registry summaries. The record identifies randomization, masking, groups, outcome summaries, and some adverse-event counts, yet does not report the original sample-size justification, detailed analysis plan, missing-data handling, or multiplicity strategy. These details affect how confidently estimates can be related to prespecified hypotheses and how completely reported analyses can be evaluated.

Finally, the planning illustrations show how sample-size requirements depend on the effect size chosen for planning. Smaller assumed effects require more participants per arm to reach the stated power targets under the stated assumptions. Because those illustrations use an observed effect from a small feasibility study, they demonstrate a planning principle rather than establishing a definitive effect size or the original design rationale.

18. 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 primary outcome is retention, which is relevant to feasibility but does not directly measure cognition. The posted information defines retention as staying in the study for 24 weeks but does not explain the operational rules for determining retention or how withdrawals and incomplete follow-up were classified. That limits interpretation of what the outcome represents in practice.

The primary confidence interval is broad and crosses no difference. This means the estimate is not precise enough to identify a clear retention contrast. The study is recorded as a phase II feasibility study, and the posted summaries do not establish that it was designed to detect a specific clinically meaningful difference in retention or in the secondary outcomes.

Important analysis details are absent. The registry record does not report the original sample-size justification, the statistical analysis plan, interim analyses, adjustment for baseline variables, missing-data methods, sensitivity analyses, or the multiplicity strategy. The primary population is described as all randomized patients, but the record does not explain how missing measurements were handled. The model behind the secondary least-squares means is also not identified.

The secondary comparisons are unadjusted, and the registry lists four outcome measures while posting two secondary outcomes. The record does not clarify the relationship between listed and posted measures or whether all planned results are represented. Safety reporting is also limited: the registry gives affected counts and selected serious-event terms, but not detailed event descriptions or context sufficient for a fuller comparison.

Finally, the registry identifies quadruple masking without explaining which roles were masked, and it provides limited information about participant selection and study conduct. These omissions constrain assessment of bias, reproducibility, and generalizability. They should be treated as limits of the available registry record, not as evidence that the unreported procedures were absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Donepezil in Female Breast Cancer Survivors With Cognitive Dysfunction — NCT01466270.
• Registry record last updated 2021-10-20; status last verified 2021-09.
• Results first posted 2015-01-09.
• 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.

22. Record Summary

The registry record describes a completed, randomized, parallel-group phase II study of donepezil hydrochloride versus placebo in female breast cancer survivors with self-reported cognitive dysfunction after chemotherapy. Enrollment is recorded as 62, with 31.0 participants in each arm for the primary outcome. The primary endpoint was mean retention at 24 weeks among all randomized patients.

Mean retention was 71.0% for donepezil and 80.7% for placebo. The unadjusted recalculated difference was 9.7 percentage points for placebo minus donepezil, with a 95% confidence interval from -11.84 to 31.24 and an unadjusted p-value of 0.377. The interval includes no difference and contrasts in either direction.

Two secondary outcomes, HVLT-IR and fatigue, are posted. The registry record does not report the original sample-size justification, detailed analysis plan, missing-data methods, or multiplicity strategy. The posted results are therefore best read as limited registry summaries with uncertainty, rather than as a complete account of the study's analysis.