Effects of Muscadine Grape Extract in Men With Prostate Cancer on Androgen Deprivation Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Muscadine Grape Extract in Men With Prostate Cancer on Androgen Deprivation Therapy (NCT03496805), a randomized phase 2 study. The primary outcome is Changes in Fatigue.

2. Clinical Question

The clinical question is whether adding muscadine grape extract (MGE) to androgen deprivation therapy (ADT) is associated with a different fatigue outcome at 6 months than adding placebo to ADT. The registry identifies recurrent prostate cancer as the condition and describes the participants as men with prostate cancer receiving ADT. Its stated aim is to assess whether MGE improves symptoms, while the posted primary endpoint focuses specifically on changes in fatigue.

The comparison is between two treatment strategies that both include ADT; it is not a comparison of ADT with no ADT. Higher PROMIS fatigue T-scores indicate more fatigue. The statistical results describe the posted group scores and their uncertainty, but do not by themselves establish why participants had those scores or whether an observed difference is important to patients.

3. Trial Design

The registry describes a phase 2, randomized, parallel-group, placebo-controlled study. Its official title identifies the study as double-blind, while the registry masking field says triple masking. The record does not specify which people were masked, so the exact masking arrangement is not reported in the registry record. The sponsor is Wake Forest University Health Sciences, and the study status is completed.

Enrollment is listed as 106. The posted results include 53 participants in the MGE group and 53 in the placebo group for the primary outcome. Participants in both groups were to receive ADT. The arm descriptions specify 4 capsules by mouth twice daily, with ADT started within 60 days before the start of MGE or placebo, respectively. The registry lists MGE as a drug intervention and placebo and ADT as other interventions.

The primary outcome is changes in fatigue at 6 months, assessed using the PROMIS Fatigue 7a Short-Form and reported as a T-score. The registry also lists secondary outcomes involving quality of life, sleep disturbance, cognitive abilities, self-reported physical function, physical performance, sub-maximal exercise, and body composition. It lists 11 outcome measures overall and 10 posted secondary outcomes.

The registry lists a start date of 2019-01-29 and a primary completion date of 2025-02-20. The original sample-size justification, the planned analysis population, and the detailed statistical analysis plan are not reported in the registry record. The study design label and the posted outcomes establish the broad comparison, but do not fill in those unreported protocol details.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Changes in Fatigue, measured over 6 months.

The primary endpoint is labeled changes in fatigue, with assessment at 6 months. It uses the PROMIS Fatigue 7a Short-Form, which asks about the experience of fatigue through 3 items and its impact through 4 items. Responses use a five-point scale from never to always. Responses are summed and transformed to a T-score, allowing fatigue to be described on a standardized metric.

Higher scores indicate more fatigue. The registry describes 50 as the population mean, with a standard deviation of 10. Its classification guidance labels scores below 50 as normal, 50–59 as mild, 60–69 as moderate, and 70 or higher as severe. These are interpretive categories for the score; the group means alone do not show how many participants fell into any category.

Fatigue is relevant to the study because the registry states that the trial aimed to assess whether adding MGE to ADT improves symptoms. A patient-reported measure can capture participants’ experience and the effect fatigue has on them, rather than relying only on an observation made by a clinician. As general context, a continuous score also allows group averages and differences to be estimated, while those averages may not describe every participant’s experience.

The posted results give group values and standard errors for the 6-month outcome. The registry does not provide the underlying participant-level scores or a breakdown of score changes by individual. Nor does it report a separate threshold for a clinically meaningful change. The result should therefore be read as a comparison of group-level fatigue scores, not as a count of participants who experienced a meaningful improvement or worsening.

7. Results Posted in the Registry

• MGE Group: mean 52.40 versus 53.40 on control; difference -1.00 (95% CI -3.49 to 1.49), standardized effect d = -0.15; z-test p = 0.432.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it is a fatigue T-score rather than a yes-or-no event. For a continuous outcome, a group mean describes the average score among participants contributing to that result. The posted means are 52.4 in the MGE group and 53.4 in the placebo group. The accompanying standard errors are 0.9 for each group. As general statistical context, a standard error describes the estimated precision of a group mean; it is not the spread of individual participants’ scores.

What does the unadjusted comparison estimate?

The simple recalculation reports a mean difference of -1.0, defined in the posted comparison as the MGE group mean relative to the placebo group mean. The negative direction corresponds to a lower average fatigue score in the MGE group. The estimate is unadjusted: it compares the posted summary statistics without accounting for covariates. This makes it a transparent summary of the group means, but it is not the same estimand or procedure as an adjusted model unless the analysis details establish that equivalence.

The recalculation also reports a pooled standard deviation of 6.552 and a standardized effect, d = -0.153. As general context, standardization expresses a mean difference in units of outcome variability, which can assist comparisons across measurement scales. The original T-score difference remains more directly interpretable in the endpoint’s own units. Standardized estimates also depend on the variability used in the denominator, so they should not be treated as independent evidence of a different clinical outcome.

How should the confidence interval and p-value be read?

The recalculated 95% confidence interval runs from -3.495 to 1.495. In general, a confidence interval communicates sampling uncertainty around an estimate using the method’s stated coverage procedure. Its endpoints mark values that are compatible with the observed data under that procedure; they are not a guarantee that the true effect lies within the particular interval. Because this interval includes zero, the unadjusted data do not rule out no difference. The unadjusted p-value is 0.432. A p-value measures compatibility with a null model, conditional on the model and assumptions; it is not a measure of clinical importance.

The registry’s reported analysis uses ANCOVA and gives p = 0.454. ANCOVA is a model-based method that can compare group outcomes while adjusting for covariates included in the model. As general context, adjustment may improve precision or account for prognostic factors when the model and covariates are appropriate. The record does not provide the adjusted estimate, its confidence interval, the covariates, or details of the model, so those aspects cannot be assessed from the registry entry. The ANCOVA result should be kept distinct from the recalculated unadjusted comparison.

What assumptions matter?

General methods for comparing means rely on assumptions about how observations relate to one another and how outcome variation is represented. Random allocation supports a comparison of assigned groups, but does not remove the need to know how outcomes were collected and analyzed. The registry record does not report diagnostic checks, model details, or the approach used for missing outcome data. No claim about whether those assumptions were met can be made from the posted summary alone.

For planning illustrations, the record specifies a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is a stated fraction of the observed effect. These are assumptions for the displayed planning calculations, not documented assumptions from the trial’s original design. General planning calculations ask how many participants would be needed under chosen assumptions; they do not describe the number actually analyzed or the probability that the trial’s result is correct.

Over-dispersion is a general concern when observed variation exceeds what a model assumes. If a model underestimates variability, standard errors can be too small and uncertainty can be understated. That concept is not a reported finding from this trial: the registry does not report an over-dispersion assessment. It is included as general statistical context, not as a characterization of the trial’s data.

The record does not report an interim-analysis plan, multiplicity adjustment, missing-data procedure, or analysis-population definition. Those details can affect how estimates and uncertainty are interpreted, particularly when multiple outcomes are measured or some observations are unavailable. Their absence from the registry record means the posted results cannot establish which procedures were used. Interpretation should remain anchored to the analyses and endpoint results that are explicitly recorded.

10. Confidence Intervals and Precision

The unadjusted mean difference is -1.0 T-score points, with a 95% confidence interval from -3.495 to 1.495. The interval crosses zero. In practical statistical terms, the posted data do not determine the direction of the population difference with precision: values on either side of zero remain compatible with this interval and the method used. The point estimate is the center of the reported comparison, but it should not be read alone as a definitive description of the underlying effect.

A confidence interval is a way to show uncertainty around an estimate. In general, it reflects the range of estimates that would be compatible with the data under the interval method and its assumptions. It does not give the probability that a particular value is true, and it does not account automatically for unreported features such as missing outcomes, analysis choices, or multiplicity. The registry does not post an adjusted confidence interval for the sponsor’s ANCOVA analysis, so precision for that adjusted estimate cannot be assessed from the posted results.

The two group standard errors are 0.9, while the pooled standard deviation used in the recalculation is 6.552. These quantities describe different aspects of uncertainty and variability: the standard error pertains to the estimated mean, while the standard deviation characterizes outcome spread. The record does not provide individual observations or additional distributional details that would allow readers to inspect the score distribution directly.

The interval’s width indicates that the estimate is not exact, and the posted result should be understood as uncertain rather than as proof of equality or proof of a difference. Whether the interval includes changes that matter to patients cannot be determined from the registry because a clinically meaningful threshold is not reported. The p-value of 0.432 offers a related summary of compatibility with a null model, but it does not replace the interval’s display of the range of plausible estimates under the analysis.

11. 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 figures are planning illustrations based on the observed effect, not the trial’s original design justification. The registry record does not report the original sample-size assumptions. For this continuous-outcome comparison, the planning calculations are stated as participants per arm, not total events. The listed figures therefore refer to the number planned in each of the two arms under each planning scenario.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect: 100%, 75%, or 50%. At 100% of the observed effect, the illustration lists 674 participants per arm for 80% power and 903 participants per arm for 90% power. At 75%, it lists 1,199 and 1,604 participants per arm, respectively. At 50%, it lists 2,696 and 3,609 participants per arm, respectively.

In plain language, the 80% power column gives the per-arm size that the calculation says would provide an 80% chance of detecting the specified effect under its assumptions, if that effect were present. The 90% power column uses a higher target chance under the same stated planning framework. Smaller effects need more participants to distinguish them from random variation, which is why the illustrations rise as the chosen fraction of the observed effect gets smaller.

These are hypothetical planning scenarios, not evidence about the probability that the completed trial detected an effect. This is not observed power. The registry does not state that these calculations were used to set the enrollment target, and they should not be interpreted as a retrospective verdict on the study’s design.

12. 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 = -1.000; pooled standard deviation σ = 6.552.
2. n = 2 × (1.96 + 0.842)² × 6.552² / -1.000² = 673.9, rounded up to 674 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 <- -1                      # observed difference in means
sigma <- 6.55209890035247                     # 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(3496805)
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 = 674 (80% power), 903 (90% power)
 75% of observed effect: n per arm = 1,199 (80% power), 1,604 (90% power)
 50% of observed effect: n per arm = 2,696 (80% power), 3,609 (90% power)
power.t.test: 674.9 
Simulated power at n = 674 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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as ANCOVA, with p = 0.454. It does not provide the ANCOVA effect estimate, confidence interval, adjustment variables, or further model details. The posted result therefore gives a p-value for that analysis but not enough information to reconstruct its adjusted comparison or assess its precision directly.

The simple recalculation from the posted group summaries is unadjusted. It gives a mean difference of -1.0, a 95% confidence interval from -3.495 to 1.495, and p = 0.432. Because an unadjusted comparison and ANCOVA can use different information and model specifications, their p-values need not be identical. The registry does not explain the difference between these results, so no specific reason for it should be inferred.

The discrepancy indicator in the record is false. The recalculation is best understood as a supplementary check based on posted summary statistics, not as a correction to the sponsor’s analysis. It cannot establish that the ANCOVA result is wrong, and it cannot replace details that are absent from the registry. Readers should keep the sponsor’s reported method and p-value separate from the unadjusted estimate and interval when interpreting the primary outcome.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 11 outcome measures overall and 10 posted secondary outcomes. These cover quality of life, sleep disturbance, cognitive abilities, self-reported physical function, physical performance, sub-maximal exercise, and body composition, in addition to the primary fatigue outcome. When multiple outcomes or comparisons are examined, the chance of obtaining at least one apparently notable result by chance can increase. As general statistical context, multiplicity procedures can address that issue, but the registry does not report whether any adjustment was planned or applied.

The record reports one primary analysis using ANCOVA and gives p = 0.454. The model details and covariates are not reported in the registry record. Nor does the record describe whether the listed outcomes were ordered in a hierarchy, whether particular outcomes were designated for confirmatory interpretation, or how secondary findings were to be handled. The presence of multiple outcomes does not itself establish that an adjustment was required or omitted; it means the approach is not available in the record for evaluation.

The registry does not report how missing outcome data were handled, how many participants contributed data to the primary analysis beyond the posted group counts, or how analysis populations were defined. The counts shown for the outcome are 53 in each group, but those counts alone do not document whether every randomized participant had an observed endpoint or how unavailable measurements were treated. No imputation method, sensitivity analysis, or reason for missingness is described.

Interim analyses and stopping rules are also not reported in the registry record. The record does not provide the original sample-size justification or a detailed statistical analysis plan. These omissions limit assessment of prespecification and robustness. They do not show that a particular procedure was or was not performed; they mark information that cannot be established from the posted registry results.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: stroke (3.8%), alanine aminotransferase increased (1.9%), cardiac arrest (1.9%), device related infection (1.9%), dizziness (1.9%).

The registry lists serious adverse events affecting 6 participants in the MGE group and 8 in the placebo group. Each group has 53 participants listed at risk for serious adverse events. It also lists other adverse events affecting 43 participants in each group, with 53 at risk in each. Deaths are listed as 1 in the MGE group and 0 in the placebo group. These are descriptive counts; they do not, by themselves, establish that an event was caused by the assigned intervention.

The registry lists Stroke at 3.8% among the top serious adverse event terms. Alanine aminotransferase increased, Cardiac arrest, Device related infection, Dizziness, and Diverticulitis are each listed at 1.9%. The record does not give the arm assignment for these terms in this summary, nor does it provide the full event narratives, timing, severity details beyond the serious-event classification, or investigators’ attribution. The term percentages should therefore be read as registry-listed frequencies, not as comparative estimates between groups.

Serious adverse events and other adverse events are separate categories in the posted results. The counts should not be added together or treated as a measure of overall risk. The registry record also does not provide a detailed account of how events were collected or adjudicated. These figures describe what is posted for the trial, without establishing comparative safety or a causal relationship.

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

The primary outcome results show group fatigue means of 52.4 for MGE and 53.4 for placebo, with standard errors of 0.9 in both groups. The unadjusted mean difference is -1.0, and its 95% confidence interval ranges from -3.495 to 1.495. The interval includes zero, and the recalculated p-value is 0.432. The sponsor’s reported ANCOVA p-value is 0.454. Together, these are statistical descriptions of the trial’s posted primary outcome; they do not establish that the groups were exactly alike or that a particular difference is meaningful.

The negative unadjusted estimate corresponds to a lower average fatigue score in the MGE group, and the score description says higher values indicate more fatigue. However, the interval leaves uncertainty about the direction and size of the underlying difference. The registry does not report a clinically meaningful threshold for change, an adjusted estimate from the sponsor analysis, or participant-level results. It is therefore not possible to determine from these results how many participants experienced a meaningful change or how the group averages relate to individual experiences.

The comparison concerns MGE plus ADT versus placebo plus ADT, not MGE in isolation or ADT versus no ADT. It should not be generalized automatically to other populations, treatment settings, outcomes, or time points. The registry lists secondary outcomes, but their results are not included in the posted primary result. The record also does not report procedures for missing data, multiplicity, or the analysis population, limiting assessment of those aspects of the evidence.

The results do not establish a treatment recommendation or prove a causal explanation for the observed scores. They document the outcome estimates and uncertainty recorded for this study. Any broader interpretation would need to consider the full trial report and relevant evidence, neither of which is detailed in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative because it places a patient-reported symptom outcome at the center of a randomized comparison. Fatigue is measured on a continuous T-score scale, allowing the result to be expressed as group means, a mean difference, and an interval rather than only as a count of participants above a threshold. That makes the size and uncertainty of the average comparison visible, while still leaving individual variation unrepresented in the mean alone.

The record also illustrates why an estimate and its precision should be considered together. The unadjusted estimate is -1.0, but the 95% confidence interval extends from -3.495 to 1.495. The sponsor’s reported ANCOVA p-value is available, yet its adjusted estimate and interval are not. Keeping those analyses distinct helps prevent an unadjusted recalculation from being mistaken for the sponsor’s model-based result.

Planning illustrations based on fractions of the observed effect show how sample-size requirements depend on the effect chosen for detection. Their assumptions are explicit, but they are not the trial’s original design assumptions. This distinction matters: retrospective planning calculations can aid understanding of precision and future study planning, but cannot establish what enrollment target was justified at the outset or whether the completed study was adequately designed.

Finally, the registry makes some limitations visible by omission. It lists multiple outcomes and adverse event counts, while important details about multiplicity, missing data, analysis populations, and model specification are not reported in the registry record. Recognizing the boundary between posted results and unreported methods is essential to a careful statistical reading.

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 record gives limited detail about the primary analysis. It reports an ANCOVA p-value but not the adjusted effect estimate, confidence interval, covariates, or full model specification. The unadjusted recalculation is based on posted group summaries and cannot recover those missing details. Consequently, readers cannot directly assess the magnitude and precision of the sponsor’s adjusted comparison from the registry entry.

The record labels the endpoint as changes in fatigue but does not provide the measurement schedule or baseline values alongside the posted group results. It is therefore not possible to determine from the registry summary how baseline and follow-up measurements were incorporated into the posted arm values, beyond the reported ANCOVA method. A clinically meaningful threshold for change is also not reported, so the practical importance of the group-level estimate cannot be judged using a prespecified threshold.

Although enrollment and outcome-group counts are listed, the registry does not describe missing-data handling, analysis-population definitions, or whether all randomized participants contributed to the analysis. It also does not report a multiplicity plan despite listing multiple outcomes, or provide an interim-analysis plan. The original sample-size justification is not reported in the registry record; the posted planning illustrations are separate from the trial’s original design assumptions.

The registry identifies triple masking in one field and double-blind in the official title, but does not specify who was masked. The adverse event summary provides aggregate counts and selected terms, without detailed attribution, timing, or arm-specific term information in the summary. These limitations do not establish flaws in the trial; they describe details unavailable in the registry record and restrict what can be concluded from it.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effects of Muscadine Grape Extract in Men With Prostate Cancer on Androgen Deprivation Therapy — NCT03496805.
• Registry record last updated 2026-03-31; status last verified 2026-03.
• Results first posted 2026-03-31.
• 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

This completed phase 2 randomized parallel-group study compared MGE with placebo among men with recurrent prostate cancer receiving ADT. Enrollment is listed as 106, with 53 participants in each posted primary-outcome group. Both arms were described as taking 4 capsules by mouth twice daily, with ADT started within 60 days before the assigned MGE or placebo.

The primary endpoint was changes in fatigue at 6 months, measured by the PROMIS Fatigue 7a Short-Form and expressed as a T-score. Posted means were 52.4 for MGE and 53.4 for placebo. The unadjusted recalculation reported a mean difference of -1.0, a 95% confidence interval from -3.495 to 1.495, and p = 0.432. The sponsor analysis was ANCOVA, with p = 0.454.

The record lists 10 secondary outcomes and aggregate adverse event counts. Details about the original sample-size justification, missing data, multiplicity, analysis populations, and several model features are not reported in the registry record.