Coenzyme Q10 in Relieving Treatment-Related Fatigue in Women With Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Coenzyme Q10 in Relieving Treatment-Related Fatigue in Women With Breast Cancer (NCT00096356), a randomized phase 1 study. The primary outcome is Effects of Coenzyme Q10 on Fatigue (as Measured by POMS-F) 24 Weeks Following Randomization.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group trial with quadruple masking. The registry record lists the study as Phase 1 and completed. Its stated purpose was to study CoQ10 for treatment-related fatigue in women with breast cancer. The trial enrolled 236 participants. The primary outcome groups reported results for 122 participants in the CoQ10 and Vitamin E arm and 114 in the placebo and Vitamin E arm; the record does not explain how those outcome counts relate to all participants enrolled.

The intervention description specifies a CoQ10 100mg capsule combined with Vitamin E 100 IU, taken orally three times per day. The comparator description is Placebo-Vitamin E 100 mg/day in 3 doses. The difference in how the record phrases the Vitamin E regimens is not explained in the registry record, so the descriptions should not be treated as proof that the schedules or doses were identical.

The primary endpoint was fatigue at 24 weeks following randomization. Quality of life measured by FACT-B and depression measured by the CES-D Short-form were also posted as outcomes at that timeframe. The registry record does not report the sequence or timing of any other assessments, treatment duration, adherence, or the criteria for including participants in each analysis. It also does not report the protocol’s original sample-size justification or design assumptions.

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: There was no run-in period. Everyone enrolled was randomized.

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.

Population: All participants

6. Primary Endpoint

The registry lists the primary outcome as Effects of Coenzyme Q10 on Fatigue (as Measured by POMS-F) 24 Weeks Following Randomization, measured over 24 weeks.

The primary endpoint was fatigue measured with the Profile of Mood States fatigue scale, abbreviated POMS-F, 24 weeks following randomization. The registry description says the scale ranges from 0 to 28 and that higher values indicate greater fatigue. The reported outcome is a continuous measure expressed as a least-squares mean, with standard errors reported for each arm. A mean describes the average score in a group, while the least-squares mean is an estimate from a model rather than necessarily a simple arithmetic average.

Fatigue was relevant to the stated trial question because the registry identifies treatment-related fatigue as the concern the intervention was intended to address. A scale gives a structured way to quantify participants’ reported fatigue and to compare group-level results. The endpoint is self-reported according to the official title. It therefore reflects participants’ responses to the measure, not an objective measurement of fatigue. The registry record does not report further details about how the scale was administered, how missing answers were handled, or what difference on the scale would be considered important to participants.

The timing matters to interpretation: the posted primary result concerns the specified assessment at 24 weeks, not every point during treatment or after follow-up. The endpoint alone cannot establish why an observed group difference arose, and it should be read together with the analysis method and the uncertainty around the estimate.

7. Results Posted in the Registry

• Arm 1 - CoQ10 & Vitamin E: mean 6.96 versus 8.33 on control; difference -1.37 (95% CI -3.45 to 0.71), standardized effect d = -0.17; z-test p = 0.197.

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.

Effects of Coenzyme Q10 on Quality of Life (as Measured by FACT-B) 24 Weeks Following Randomization

• 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 1 - CoQ10 & Vitamin E: mean 111.80 versus 109.80 on control; difference 2.00 (95% CI -3.23 to 7.23), standardized effect d = 0.10; z-test p = 0.453.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1 - CoQ10 & Vitamin E and the control. The interval gives the range of effects that remain compatible with the data.

Effects of Coenzyme Q10 on Depression (as Measured by CES-D Short-form) 24 Weeks Following Randomization

• 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 1- CoQ10 & Vitamin E: mean 11.70 versus 12.40 on control; difference -0.70 (95% CI -3.49 to 2.09), standardized effect d = -0.06; z-test p = 0.623.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1- CoQ10 & Vitamin E and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes address quality of life, measured with FACT-B, and depression, measured with the CES-D Short-form, at 24 weeks following randomization. Across these outcomes, the estimates do not establish a clear between-group difference: the sponsor-reported confidence intervals include the null. The estimates vary in direction, and their precision is limited. The secondary results therefore do not provide a consistent, precise pattern that changes the interpretation of the primary fatigue result.

These outcomes complement the primary endpoint by describing other aspects of participants’ reported experience. They are not substitutes for the primary fatigue measure, and their results should be considered as separate analyses rather than combined into a single conclusion. The registry lists two secondary outcomes, but does not report a hierarchy among them, a prespecified strategy for interpreting them jointly, or a multiplicity adjustment.

When several outcomes are tested, the chance of obtaining at least one apparently notable result can increase, even if there are no underlying effects. Adjustment methods or a prespecified testing order can address this issue, but the registry record does not report whether either was used. Consequently, unadjusted secondary findings generally carry less weight than a prespecified primary result, especially when interpreting isolated p-values. That caution does not mean the secondary measures are irrelevant; it means the evidence should be read in context and with appropriate attention to the number of comparisons.

The secondary outcomes are reported at the same stated follow-up timeframe as the primary endpoint, which allows a broad comparison of the reported assessment period. The record does not provide enough detail to determine whether all participants contributed to each outcome or whether missing responses differed between arms. The secondary pattern should therefore be treated as descriptive of the posted analyses, not as a complete account of every possible outcome or time point.

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

• Effects of Coenzyme Q10 on Quality of Life (as Measured by FACT-B) 24 Weeks Following Randomization
• Effects of Coenzyme Q10 on Depression (as Measured by CES-D Short-form) 24 Weeks Following Randomization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s fatigue measure is represented by a score, and the arm-level results are expressed as least-squares means. A mean difference compares the estimated average scores between groups. Its sign depends on the subtraction order; the posted comparison is CoQ10 minus placebo. Since higher POMS-F scores indicate greater fatigue, a negative difference points toward a lower estimated fatigue score in the CoQ10 arm. That direction describes the estimate and does not establish its precision or importance.

What does the least-squares mean represent?

A least-squares mean is a model-based estimate of an arm’s mean outcome. It can differ from a raw arithmetic average when the analysis accounts for features of the data or study design. The registry gives the outcome parameter as a least-squares mean but does not report the full model specification, covariates, repeated-measure structure, or missing-data assumptions. The sponsor’s analysis is labelled Mixed Models Analysis, but its detailed model terms and implementation are not reported in the registry record. As a result, the posted label identifies a general analysis approach without allowing a complete independent reconstruction of the sponsor’s model.

How should the standard errors be read?

The arm-level results report standard errors. A standard error describes the statistical uncertainty in an estimated mean; it is not the spread of individual participants’ scores. In general, a smaller standard error indicates a more precisely estimated mean, while a larger one indicates greater uncertainty. Standard errors depend on both the variability in the outcome and the information available for estimating the mean. The reported standard errors should not be mistaken for standard deviations or for confidence limits.

What does the mean-difference interval add?

A confidence interval expresses uncertainty around the estimated between-group difference. It is more informative than the point estimate alone because it shows a range of effects compatible with the data under the analysis assumptions. If an interval includes the null value of no difference, the data do not distinguish that value from the other values in the interval at the corresponding confidence level. The sponsor-reported primary interval crosses the null. Its span indicates that the estimate is not precise enough to settle whether the underlying difference is in one direction, absent, or in the other direction.

What is the role of the p-value?

A p-value assesses how unusual the observed result, or a more extreme result, would be under a specified null hypothesis and the model assumptions. It does not measure the size of an effect, and it is not a direct measure of clinical importance. It also does not give the probability that a result is due to chance. The registry posts a sponsor p-value for the primary comparison and an unadjusted recalculation based on posted summary statistics. Those analyses are not identical in method: a model-based analysis may use information not contained in group means and standard errors alone. The recalculation is therefore a simple unadjusted comparison, not a replacement for the sponsor’s analysis.

Why can over-dispersion matter?

Over-dispersion is a general concern when observed variability exceeds what an assumed statistical model allows. It is particularly relevant to outcomes whose variability is modeled with a distribution that expects a specific mean-variance relationship. If variability is larger than expected, standard errors and tests based on the narrower model can be too optimistic unless the analysis accounts for that extra variation. The primary endpoint is continuous, and the registry does not report a specific over-dispersion assessment. This general concept should not be taken as evidence that over-dispersion occurred in this trial.

What can be inferred from the posted methods?

Randomization is intended to create comparable groups at allocation, and masking is intended to reduce the influence of expectations on treatment delivery, outcome assessment, or analysis. The registry lists randomization and quadruple masking, but does not define which roles were masked or report details of allocation concealment. The trial is described as parallel-group, so the posted comparison is between separate groups rather than a within-participant crossover. These design labels support understanding of the comparison but do not substitute for information about execution, adherence, attrition, or the analysis population.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a mean difference of -1.37 POMS-F units, with a 95% confidence interval from -3.39 to 0.64. The interval crosses the null value of no difference, so the posted result is compatible with a range of effects on both sides of the null under the sponsor’s analysis. In practical terms, the point estimate alone should not be read as a precise statement of the difference that would be expected in a broader population.

A confidence interval is not a range that contains a fixed proportion of individual participants’ scores. It describes uncertainty in an estimated group contrast under a statistical model and its assumptions. The 95% label describes the long-run coverage property of the procedure when its assumptions hold; it does not mean that there is a 95% probability that this particular interval contains the true effect.

The size of the interval matters alongside its position. An interval that crosses the null leaves uncertainty about whether the underlying group difference is below, at, or above that null. The estimate’s direction may be noted, but the interval does not support treating that direction as settled. Nor does an interval crossing the null prove equivalence: equivalence requires a prespecified margin and an analysis designed to assess whether effects are contained within that margin. Such a margin is not reported in the registry record.

The registry gives standard errors for each arm as well as the sponsor’s interval for the group difference. These are different quantities: arm-level standard errors describe uncertainty in each estimated mean, while the confidence interval for the difference describes uncertainty in the contrast. The confidence interval is the more direct measure for assessing precision of the between-arm comparison. It remains conditional on the analysis and assumptions, and the record does not provide all model details needed to evaluate those assumptions fully.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s own original design assumptions. They give participants per arm for this continuous-outcome comparison; they are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario targets the stated fraction of the observed effect.

The 80% power column represents the planned number of participants per arm under those assumptions for a design with an 80% probability of detecting the effect used in that scenario if that effect were the true one and the assumptions held. The 90% column makes the corresponding illustration for a 90% probability. These are design probabilities under assumptions, not probabilities that the present trial’s result is correct.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so it requires more participants under the same planning assumptions. The larger figures in the smaller-effect scenarios reflect that relationship. These estimates use an effect observed in this trial as their starting point; they are not independent evidence about what effect future research should expect.

The trial’s own sample-size justification, original target effect, and original power assumptions are not reported in the registry record. The displayed planning figures therefore should not be used to infer that the trial was designed for a particular power or that it had adequate power for the primary question. This is not observed power.

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 = -1.370; pooled standard deviation σ = 8.134.
2. n = 2 × (1.96 + 0.842)² × 8.134² / -1.370² = 553.3, rounded up to 554 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 <- -1.37                      # observed difference in means
sigma <- 8.13381156643616                     # 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(96356)
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 = 554 (80% power), 741 (90% power)
 75% of observed effect: n per arm = 984 (80% power), 1,317 (90% power)
 50% of observed effect: n per arm = 2,214 (80% power), 2,964 (90% power)
power.t.test: 554.3 
Simulated power at n = 554 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis is a Mixed Models Analysis of the mean difference in final values. It estimates a difference of -1.37, with a 95% confidence interval from -3.39 to 0.64 and p = 0.181. The posted summary-statistic re-calculation also estimates a difference of -1.37, but it is a simple unadjusted re-calculation based on the reported group summaries rather than the sponsor’s mixed-model analysis.

The re-calculation is useful as a transparent check on the basic direction and scale of the contrast, but it does not reproduce the sponsor’s model. The methods use different information and assumptions, and small differences in interval or test results can arise for that reason. The record marks no discrepancy between the two analyses. The sponsor’s own analysis remains the appropriate result to quote as the registry-reported analysis; the recalculation is supplementary and should not be presented as a corrected sponsor result.

Both analyses point to an estimated difference in the direction of a lower fatigue score in the CoQ10 arm, while the sponsor’s interval includes the null. The central interpretation should therefore focus on the estimate’s uncertainty rather than treating the sign alone as conclusive. The registry does not report the full mixed-model specification, so the sponsor analysis cannot be independently reconstructed from the posted summary information alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study makes several statistical comparisons. Even when each test is considered separately, conducting multiple tests can increase the chance of a false-positive finding somewhere among them. This trial has a primary fatigue endpoint and two posted secondary outcomes, but the registry record does not report a multiplicity adjustment, a testing hierarchy, or a rule for interpreting the secondary results alongside the primary one. It is therefore not possible to determine from the record whether the reported p-values were adjusted or how the outcome family was handled in the protocol.

The record also does not report the number of participants with missing primary or secondary outcome measurements, reasons for missingness, or methods used to handle missing data. It does not state whether the analyses followed an intention-to-treat population, a per-protocol population, or another analysis population. Although arm-level outcome counts are posted, the record does not explain participant flow from enrollment through each analysis. Without that information, the potential influence of missing data and exclusions cannot be assessed.

The sponsor labels the primary analysis Mixed Models Analysis. Some mixed-model approaches can use available repeated measurements under specified assumptions, but the registry does not provide enough detail to establish whether repeated measurements were modeled, what assumptions were used, or how departures from those assumptions were addressed. The analysis label alone cannot answer those questions.

The registry record does not report interim analyses, stopping rules, or the original sample-size calculation. It also does not report a protocol-defined threshold for a clinically important difference on the fatigue scale. These omissions do not establish that the trial lacked such procedures; they mean the information is not reported in the registry record. They limit independent evaluation of the analysis plan and of how the posted outcomes relate to the trial’s original objectives.

16. 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: anc (11.0%), wbc (4.0%), fatigue (3.2%), infection (3.2%), nausea (3.2%).

The registry posts serious adverse event counts for participants at risk in each arm: 22 of 100 in the CoQ10 and Vitamin E group, and 15 of 93 in the placebo and Vitamin E group. It also posts other adverse event counts of 89 of 100 and 84 of 93, respectively. These are event summaries with their own at-risk counts; they should not be confused with the primary outcome analysis counts or interpreted as a comparison adjusted for follow-up time.

The record lists ANC, WBC, fatigue, infection, nausea, and dehydration among the leading serious adverse event terms, with the posted percentages attached to those terms. The meanings of ANC and WBC, event definitions, severity criteria, and the period over which events were collected are not reported in the registry record. The posted term list should therefore be read as a registry summary, not as a detailed clinical adjudication.

Death counts are not reported in the registry record. The adverse event figures alone do not establish comparative safety, and the registry summary does not provide enough detail about exposure time, event recurrence, attribution, or statistical analysis to support a broader safety conclusion. These counts describe the posted record and should not be used as medical advice.

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

The posted primary result describes a group-level fatigue score comparison at 24 weeks following randomization. The estimated difference is in the direction of a lower mean fatigue score in the CoQ10 and Vitamin E arm than in the placebo and Vitamin E arm. The sponsor-reported confidence interval includes the null and spans values on both sides of it. Thus, the registry result does not establish a clear difference between groups, while also not proving that the groups are identical.

The result does not establish whether a difference of this size would matter to participants. The registry record does not report a threshold for a clinically important change in POMS-F. Nor does the result describe what an individual participant experienced: group averages do not indicate that every person in an arm had a similar score or response. The scale is self-reported, and the posted analysis concerns a specified assessment rather than all possible experiences during or after treatment.

The trial compares the combination of CoQ10 and Vitamin E with placebo and Vitamin E as described in the registry. It cannot isolate an effect attributable only to CoQ10 if the groups differ in other aspects of their regimens or in how those regimens were implemented. The record’s descriptions of the Vitamin E regimens are not fully aligned, and it does not clarify that issue. This makes it important not to overstate what component the comparison identifies.

The primary and secondary results should also be understood in light of incomplete reporting about the analysis plan, missing outcomes, and participant flow. These limitations concern how fully the posted result can be evaluated; they do not alter the numerical estimate. The evidence describes this trial’s recorded comparison and does not by itself establish what would happen in other populations, settings, or treatment circumstances.

No treatment recommendation follows from these statistics. The result is an estimate with uncertainty, drawn from a randomized comparison reported in the registry. Its appropriate meaning is bounded by the specified population, interventions, outcome measure, follow-up assessment, and the details that the registry does and does not report.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment estimate should be read together with its uncertainty. The primary point estimate has a direction, but the sponsor-reported confidence interval crosses the null. Reporting only the point estimate could make the evidence seem more definite than it is; reporting only that the result was not statistically significant could obscure the range of values that remains compatible with the data.

It also illustrates the distinction between sponsor analysis and summary-statistic re-calculation. A simple unadjusted calculation can help readers understand the basic contrast, but it is not a substitute for a model-based analysis when the sponsor’s model may use additional information. The record’s outcome means and standard errors do not reveal every detail of the mixed-model analysis, so methodological transparency matters for reproducibility.

The trial also includes multiple outcomes, each of which contributes a different perspective on participants’ reported experience. Without a reported multiplicity strategy, secondary findings require cautious interpretation. Likewise, limited reporting about missing data and analysis populations makes it difficult to assess how completely the posted outcomes represent enrolled participants.

Finally, planning calculations based on an observed effect are useful illustrations of how the target effect size influences required sample size, but they are not evidence about the trial’s original design or its observed power. Keeping those planning concepts separate from the actual trial analysis helps prevent retrospective calculations from being mistaken for design documentation.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific reporting gaps limit interpretation. The registry does not give detailed eligibility criteria, participant characteristics, treatment adherence, or the participant flow into the primary and secondary analyses. Although enrollment and outcome-group counts are posted, the reasons for any difference between those counts are not reported in the registry record. The record also does not explain how missing scores were handled or identify the analysis population.

The intervention descriptions leave some uncertainty about the comparison. The CoQ10 arm is described as CoQ10 100mg combined with Vitamin E 100 IU three times per day, while the placebo arm is described as Placebo-Vitamin E 100 mg/day in 3 doses. The registry does not clarify the difference in these Vitamin E descriptions. It also does not report treatment duration or adherence, limiting assessment of the exposure represented by the 24-week outcome.

The sponsor reports a Mixed Models Analysis, but the full model specification, covariates, repeated-measure structure, and assumptions are not reported in the registry record. A complete independent reconstruction of that analysis is therefore not possible from the posted summary. The registry also does not report a clinically important difference threshold for POMS-F, so the practical importance of the estimated difference cannot be determined from the posted result.

Other limitations include the absence of a reported multiplicity plan for secondary outcomes, details of interim analyses or stopping rules, and the original sample-size justification. The adverse event record does not provide event definitions, follow-up duration, attribution, or death counts. These are limitations in what is documented in the registry record; they should not be mistaken for evidence that the procedures or information did not exist elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Coenzyme Q10 in Relieving Treatment-Related Fatigue in Women With Breast Cancer — NCT00096356.
• Registry record last updated 2021-09-29; status last verified 2021-09.
• Results first posted 2014-12-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed randomized, double-blind, placebo-controlled, parallel-group Phase 1 trial of CoQ10 with Vitamin E versus placebo with Vitamin E in women with breast cancer and treatment-related fatigue. Enrollment was 236, and quadruple masking is listed. The primary endpoint was POMS-F fatigue at 24 weeks following randomization.

The sponsor reported a mean difference in final fatigue values of -1.37, with a 95% confidence interval from -3.39 to 0.64 and p = 0.181. The interval includes the null, leaving uncertainty about the direction and size of any underlying difference. Quality of life and depression were also posted as secondary outcomes at the same timeframe. Important details about missing data, analysis populations, multiplicity, and the original design assumptions are not reported in the registry record.