Using Soy Estrogens to Prevent Bone Loss and Other Menopausal Symptoms: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Using Soy Estrogens to Prevent Bone Loss and Other Menopausal Symptoms (NCT00076050), a randomized phase 3 study. The primary outcome is Change From Baseline in Bone Mineral Density.

2. Clinical Question

The primary comparison is reported as a mean difference of 0.014 g/cm2, with a 95% confidence interval from -0.022 to 0.050 and an unadjusted p-value of 0.45. The interval includes no difference and also allows values in either direction. These statistics describe the posted comparison; they do not establish that the supplement prevented bone loss or had an effect on symptoms. The endpoint title identifies change from baseline, but the registry does not provide a description explaining precisely how the posted arm means correspond to that change. That reporting detail matters when interpreting the estimate.

3. Trial Design

The registry identifies this as a Phase 3, randomized, triple-masked, parallel-group trial. The study is marked completed. Its listed start date is 2003-09 and its primary completion date is 2009-03. The sponsor is the University of Miami. Enrollment is reported as 248; that registry enrollment figure is not the same as the number contributing to each posted outcome.

The two listed arms received either soy isoflavones or placebo daily over 2 years. The soy arm description specifies 200 mg daily. For the primary outcome, the posted summary reports a mean for 99 participants in the soy isoflavone group and 83 in the placebo group. These outcome-specific counts should not be assumed to explain enrollment or to represent every participant randomized. The registry does not report why the outcome counts differ from the enrollment figure, or how missing observations were handled.

Randomization and masking are features intended to reduce systematic differences in treatment assignment and outcome assessment. The record does not state who was masked, how the allocation sequence was generated or concealed, or whether masking was maintained. It also does not report the trial's original sample-size justification, planned analysis population, or statistical analysis plan. Those details cannot be inferred from the trial's Phase 3 label or from the planning illustrations based on observed results.

The primary endpoint is listed as change from baseline in bone mineral density, measured in g/cm2, with a timeframe of baseline and 2 years. The registry lists changes in Women's Health Questionnaire Score and change in Vaginal Maturation Value as secondary outcomes, also with a baseline-and-2-years timeframe. The record lists three outcome measures but posts results for the primary outcome and these two secondary outcomes. It does not give further endpoint definitions or describe the procedures used to measure them.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Bone Mineral Density, measured over baseline and 2 years.

Bone mineral density is a measure of the amount of mineral in bone over a measured area. The registry names change from baseline in bone mineral density as the primary endpoint and gives g/cm2 as the unit. Comparing change over the stated baseline-and-2-years timeframe is relevant to the study's stated question about bone loss: the outcome is intended to capture how the measured bone density changes during the trial, rather than only its value at a single time.

The posted primary results give group means of 1.146 g/cm2 for the soy isoflavone group and 1.132 g/cm2 for the placebo group, with standard deviations of 0.125 and 0.124, respectively. The reported comparison is a mean difference of 0.014 g/cm2. However, the registry's endpoint title says “Change From Baseline,” while its result description is empty and the posted values are presented as means. The record does not explain whether these arm means represent change scores, follow-up measurements, or another summary of the endpoint. That ambiguity limits interpretation of the values as change specifically.

Using a continuous measure allows the result to be expressed as a difference in the outcome's original units, alongside a confidence interval. The estimate and its interval describe the observed comparison and its uncertainty; they do not, by themselves, establish a clinical threshold or a treatment benefit. The registry does not report a threshold for a meaningful difference in bone mineral density.

7. Results Posted in the Registry

• Soy Isoflavone Group: mean 1.15 versus 1.13 on control; difference 0.01 (95% CI -0.02 to 0.05), standardized effect d = 0.11; z-test p = 0.450.

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.

Changes in Women's Health Questionnaire Score

• 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:
  • Soy Isoflavone Group: mean -0.73 versus -0.34 on control; difference -0.39 (95% CI -2.23 to 1.45), standardized effect d = -0.06; z-test p = 0.678.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Soy Isoflavone Group and the control. The interval gives the range of effects that remain compatible with the data.

Change in Vaginal Maturation Value

• 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:
  • Soy Isoflavone Group: mean 0.20 versus -1.78 on control; difference 1.98 (95% CI -5.50 to 9.46), standardized effect d = 0.08; z-test p = 0.604.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Soy Isoflavone Group and the control. The interval gives the range of effects that remain compatible with the data.

The two secondary outcomes address different aspects of menopausal change from the primary bone mineral density endpoint. The Women's Health Questionnaire Score concerns a questionnaire measure, while Vaginal Maturation Value is a separate score. Their posted group comparisons have confidence intervals spanning zero, as does the primary comparison. Taken together, the secondary summaries do not create a consistent pattern that resolves the uncertainty in the primary result or establishes a clear difference across these outcomes.

These measures are related to the study's broader interest in menopausal symptoms, but they are not substitutes for the primary bone mineral density endpoint. Each measure has its own definition, units, variability, and comparison. A result on one cannot be used to infer a result on another, and the registry does not report a joint analysis connecting the secondary outcomes with bone mineral density. The endpoint definitions and their measurement details are not fully described in the record.

The secondary comparisons are unadjusted. In general, testing multiple outcomes creates more opportunities for apparently notable results by chance. A multiplicity procedure can control the overall error rate across a family of tests, but it requires a prespecified strategy about which outcomes and comparisons are included. The registry record does not report such a strategy or provide sponsor-reported secondary analyses. Accordingly, unadjusted secondary results carry less confirmatory weight than a result from a prespecified, appropriately controlled analysis.

The posted results are best treated as descriptive evidence about the observed comparisons, not as independent confirmations of a treatment effect or of its absence. The registry does not report whether these outcomes were powered as separate objectives, how missing data were handled, or whether analyses were adjusted. Those omissions limit claims about the secondary findings and about how they should be weighed alongside the primary endpoint.

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

• Changes in Women's Health Questionnaire Score
• Change in Vaginal Maturation Value

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous outcome, a group mean describes the average recorded value in that group. The standard deviation describes how dispersed individual observations are around their group mean; it is not the standard error of the mean. In the primary results, the means are 1.146 g/cm2 and 1.132 g/cm2, and the corresponding standard deviations are 0.125 and 0.124. The comparison reports a mean difference of 0.014 g/cm2. The direction of a difference depends on the order of subtraction; the posted comparison is for soy isoflavones relative to placebo.

What does the confidence interval describe?

A confidence interval expresses uncertainty around an estimated difference. In general, a confidence interval is constructed by a method that would cover the underlying parameter at its stated rate over repeated use of that method, if its assumptions hold. It is not a range containing a known proportion of individual participant values, nor is it a probability statement about this particular interval after it has been calculated. The primary interval, -0.022 to 0.050 g/cm2, includes zero and permits estimates in either direction. Its width indicates that the point estimate alone should not be treated as precise.

What does the p-value add?

The unadjusted p-value is 0.45. In general, a p-value measures how surprising data at least as inconsistent with a null hypothesis would be if that hypothesis and the test's assumptions held. It does not measure the probability that the null hypothesis is true, the chance that a finding is due to chance, or the clinical importance of an estimate. A large p-value does not demonstrate equivalence or rule out an effect. The registry does not report the original analysis plan or threshold used by the trial investigators. Consequently, the posted p-value should be read as an unadjusted summary statistic, not as a complete account of the trial's planned inference.

Why does the distinction between standard deviation and standard error matter?

Standard deviation describes variation among observations; standard error describes uncertainty in an estimated quantity, such as a mean. They answer different questions. The primary endpoint is reported with standard deviations. The secondary endpoints are reported with standard errors, so their spread values should not be interpreted as participant-to-participant variation. A standard error is generally smaller when a mean is estimated more precisely, but its interpretation depends on the calculation and the data structure. The registry does not provide additional detail about the secondary-outcome standard-error calculations.

How should the posted comparisons be understood?

The comparison estimates are recalculated from posted summary statistics and are unadjusted. They do not incorporate covariates or account for any analysis features that are not present in the registry record. The registry reports no outcome analysis records for these results. The recalculated confidence intervals and p-values therefore should not be mistaken for sponsor-reported model results. There is no discrepancy flag, so the stated precedence rule for a disagreement with sponsor analyses is not triggered; no sponsor analysis details are posted to compare.

General statistical interpretation also depends on how the outcome was defined, which participants were analyzed, and how missing observations were treated. Those details can affect both estimates and uncertainty. The primary endpoint's title specifies change from baseline, but the registry does not explain how that definition maps to the posted means. The record likewise does not report the analysis population, missing-data handling, or a model specification. These are limits on what can be concluded from the available summaries, not grounds for assuming a particular method.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. If a model assumes less variation than the data contain, its uncertainty estimates can be too small and its confidence intervals too narrow. Methods that account for over-dispersion can provide more appropriate uncertainty estimates when the outcome and model require them. This is a general point about statistical modeling, not a claim about this trial: the primary outcome is continuous, and the registry does not describe a model for which over-dispersion was assessed. No conclusion about its presence or treatment in the analysis can be drawn from the record.

Overall, the most direct reading is to pair the mean difference with its confidence interval and to keep the distinction between posted-summary recalculations and trial-reported analyses in view. Statistical evidence, uncertainty, endpoint definition, and analysis transparency all contribute to interpretation; none should be replaced by a p-value alone.

11. Confidence Intervals and Precision

The primary mean difference is 0.014 g/cm2, with a 95% confidence interval from -0.022 to 0.050. This interval is compatible with a negative difference, a positive difference, and zero. It therefore does not pin down the direction of the underlying group difference. The interval is also important for judging precision: although the point estimate is near zero, the range of compatible values is appreciably broader than that single estimate.

In general, a confidence interval combines the estimated effect with its sampling uncertainty under a statistical method and its assumptions. A narrower interval indicates greater precision for the parameter being estimated; it does not guarantee that the estimate is unbiased or that the endpoint is clinically meaningful. A wider interval leaves more possible values consistent with the data. The primary interval's inclusion of zero is not proof of no effect, just as inclusion of positive values is not proof of benefit.

The reported outcome counts are 99 in the soy isoflavone group and 83 in the placebo group. The registry does not explain the relation between these counts and its enrollment figure, nor whether the same participants contributed to every measure. It also does not report the handling of missing outcomes. These details matter because the information contributing to an estimate affects its precision and may affect its interpretation.

The registry provides no prespecified threshold for a clinically important difference and no equivalence margin. The interval therefore supports a statement about statistical uncertainty, not a conclusion that all values within it are clinically negligible or important. The endpoint description also does not clarify whether the posted means are change scores, despite the endpoint title. The uncertainty interval can be read as an interval around the posted comparison, but it cannot resolve that definition issue.

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 illustration is not the trial's original design calculation. For the primary endpoint, its figures are participants per arm, not total events. It assumes 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 the stated fraction of the observed effect. The registry does not report the trial's original sample-size assumptions or justification.

The 80% power column describes the illustrative number of participants per arm needed for an 80% chance of detecting the selected effect under those assumptions, if that effect is real and the calculation's assumptions apply. The 90% column describes the corresponding planning target for a 90% chance. These are planning probabilities under a specified model, not guarantees about a future study. They are not observed power.

For the primary comparison, the illustration uses 1,243 participants per arm for 80% power and 1,664 per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 2,209 and 2,957 per arm; for 50%, they are 4,970 and 6,653 per arm. Smaller effects require more participants because they are harder to distinguish from random variation under the same assumptions.

The observed effect is estimated from the trial's posted results, so these figures are not evidence that the trial was designed around those assumptions. Planning based on an observed effect can be especially uncertain when the estimate itself is imprecise. The illustration should be read as a conditional planning exercise, not as a retrospective judgment about the trial's success or adequacy.

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 = 0.014; pooled standard deviation σ = 0.125.
2. n = 2 × (1.96 + 0.842)² × 0.125² / 0.014² = 1,242.3, rounded up to 1,243 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 <- 0.014                      # observed difference in means
sigma <- 0.124545440168104                     # 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(76050)
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 = 1,243 (80% power), 1,664 (90% power)
 75% of observed effect: n per arm = 2,209 (80% power), 2,957 (90% power)
 50% of observed effect: n per arm = 4,970 (80% power), 6,653 (90% power)
power.t.test: 1243.3 
Simulated power at n = 1,243 per arm: 0.802 (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

Multiplicity arises when several outcomes, comparisons, time points, or analyses are examined. In general, the more statistical tests considered, the greater the opportunity for at least one apparently unusual result to arise by chance if no underlying effects are present. Prespecifying a testing hierarchy or using an adjustment can help control this problem, but the appropriate approach depends on the questions and analysis plan.

The registry lists a primary outcome and two secondary outcomes. It posts unadjusted comparisons for these measures, but the record does not report a multiplicity plan, a hierarchy among outcomes, or an adjustment for multiple testing. It also reports no analysis records. The available p-values should therefore not be read as multiplicity-adjusted or as a complete account of the investigators' planned testing. This is particularly relevant when interpreting secondary outcomes, which are generally less confirmatory when considered without a reported adjustment strategy.

The record does not report how missing data were handled, whether all randomized participants were included in the primary analysis, or whether any imputation or sensitivity analyses were conducted. The posted primary outcome counts are 99 for the soy isoflavone group and 83 for placebo, while enrollment is 248. The registry does not explain the relationship among these figures. It is not possible to determine from the record whether differences reflect missing measurements, analysis eligibility, or another reason.

The analysis population is not reported in the registry record. Nor does the record specify whether analyses followed an intention-to-treat principle, a per-protocol approach, or another population definition. These terms describe choices about which participants contribute to an analysis; they should not be assigned to this trial without documentation. The endpoint title identifies change from baseline, but the record does not explain the calculation or the handling of observations that may not have been available at both time points.

These reporting gaps do not establish that the trial lacked a multiplicity or missing-data plan. They mean that readers cannot assess those features from the registry record. They also prevent a full evaluation of how analysis decisions may have influenced the estimates and their uncertainty.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fracture (5.7%), breast cancer (0.8%), leukemia (0.8%).

The registry reports serious adverse events affecting 9 of 122 participants at risk in the soy isoflavones group and 3 of 126 at risk in the placebo group. Other adverse events are reported as affecting 121 of 122 participants at risk in the soy group and 122 of 126 at risk in the placebo group. These are the registry's counts; the record does not provide an adjusted comparison or a statistical test for these safety summaries.

The serious-event terms listed include fracture at 5.7%, breast cancer at 0.8%, and leukemia at 0.8%. The registry does not specify in this summary whether those percentages are arm-specific, nor does it provide further detail about timing, severity classification, or attribution. The event terms should not be interpreted as evidence that the study treatment caused or prevented them.

Deaths are not reported in the registry record. The adverse-event figures are counts of participants affected, not a complete description of every event or its clinical context. Differences in the reported counts alone do not establish a safety difference, particularly without details on ascertainment, follow-up, and analysis. These summaries describe what the record reports and do not support individual medical decisions.

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

The primary comparison reports a mean difference of 0.014 g/cm2, with a 95% confidence interval from -0.022 to 0.050 and an unadjusted p-value of 0.45. This is an estimate from posted summary statistics. Its interval includes no difference and values on either side of zero, so the result does not determine a clear direction or precise size of the group difference.

That statistical result does not show that soy isoflavones prevented bone loss, nor does it establish that they had no effect. A non-significant p-value is not evidence of equivalence, and the registry does not report an equivalence margin. The record also does not state a threshold for a clinically important difference. The estimate should not be translated into a claim of clinical benefit or lack of benefit.

The registry describes change from baseline in bone mineral density as the primary outcome, but does not explain how the reported arm means correspond to that change. This makes the endpoint's numerical interpretation less certain. The record also does not report the analysis population, missing-data approach, statistical model, original sample-size justification, or multiplicity strategy. Those details could inform how the results should be interpreted, but they cannot be reconstructed from the posted summaries.

The two secondary comparisons likewise do not settle the primary question. They concern different measures, and their unadjusted results should not be treated as independent confirmation. The safety summaries describe reported adverse events but do not establish causation or provide a full comparative safety analysis.

Overall, the posted data characterize a comparison with substantial uncertainty and incomplete analysis detail. They can inform discussion of the measured outcomes and the precision of their estimates, but they cannot establish a treatment effect, rule one out, or answer whether any observed difference would matter clinically. The registry's stated study hypothesis is not itself evidence that the hypothesis was supported.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be interpreted alongside its uncertainty. The primary mean difference is 0.014 g/cm2, but its confidence interval ranges from -0.022 to 0.050. Reporting only the estimate would obscure that the data remain compatible with differences in either direction. The unadjusted p-value of 0.45 is another summary, not a replacement for the interval or for a clear account of the endpoint.

It also highlights the importance of matching a result to its endpoint definition. The primary outcome is named as change from baseline, while the registry does not explain the relationship between that label and the posted means. Without that information, even a carefully read numerical estimate has limits. Transparent descriptions of outcome calculations, analysis populations, and missing-data methods are essential for assessing what an estimate represents.

The registry's planning illustrations show another statistical distinction: planning for a smaller target effect requires more participants per arm under the stated assumptions. Those illustrations use the observed effect and should not be confused with the trial's original design or with observed power. Keeping those purposes separate helps prevent retrospective calculations from being mistaken for evidence about the design or result.

Finally, the secondary outcomes and adverse-event summaries emphasize that a trial can report several kinds of evidence that answer different questions. Unadjusted secondary comparisons do not automatically confirm a primary finding, and adverse-event counts alone do not establish causation. Together, these features make the record a useful example of how estimates, uncertainty, endpoint clarity, multiplicity, and reporting completeness shape statistical interpretation.

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 registry provides limited detail about the primary endpoint. It labels the measure as change from baseline in bone mineral density, gives a baseline-and-2-years timeframe, and posts arm means, but supplies no endpoint description explaining how those values represent change. This makes the clinical meaning of the numerical comparison less transparent.

The posted primary outcome counts differ from the enrollment figure, and the registry does not explain why. It does not state the analysis population, whether all randomized participants were included, or how missing measurements were handled. The record also does not report a statistical model, covariate adjustment, or sensitivity analyses. These omissions limit assessment of potential bias and of the robustness of the estimate.

The trial's original sample-size rationale and analysis plan are not reported. The planning illustrations are based on the observed effect and explicit generic assumptions; they do not establish the design assumptions used by investigators. The registry also does not describe a multiplicity approach for the primary and secondary outcomes. The posted secondary comparisons are unadjusted, and the record contains no sponsor-reported analysis entries.

Further interpretive limits include the absence of a stated threshold for a clinically important difference and the lack of detail about what the posted adverse-event percentages represent. Deaths are not reported in the registry record. The record does not provide additional context for the serious-event counts or state whether events were judged related to the intervention.

These are limitations of the information in the registry record. They should not be taken as proof that the trial investigators did not collect or analyze the relevant information; the record simply does not report it.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Using Soy Estrogens to Prevent Bone Loss and Other Menopausal Symptoms — NCT00076050.
• Registry record last updated 2016-12-06; status last verified 2016-10.
• Results first posted 2016-12-06.
• 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.

22. Record Summary

NCT00076050 is a completed Phase 3 randomized, triple-masked, parallel-group trial sponsored by the University of Miami. It compared daily soy isoflavones, specified as 200 mg, with daily placebo over 2 years in women who had recently gone through menopause. Enrollment is reported as 248.

The primary outcome is listed as change from baseline in bone mineral density, measured in g/cm2. The posted comparison is a mean difference of 0.014, with a 95% confidence interval from -0.022 to 0.050 and an unadjusted p-value of 0.45. The interval includes zero, and the registry does not explain how the posted means correspond to the endpoint's change-from-baseline label.

Two secondary outcomes are reported, along with adverse-event summaries. The registry does not report an analysis plan, multiplicity strategy, missing-data approach, analysis population, or the original sample-size justification. The displayed planning figures are illustrations based on the observed effect and stated assumptions, not the trial's own design record.