Armodafinil in Treating Fatigue Caused By Radiation Therapy in Patients With Primary Brain Tumors: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Armodafinil in Treating Fatigue Caused By Radiation Therapy in Patients With Primary Brain Tumors (NCT01032200), a randomized phase 2 study. The primary outcome is Retention.

2. Clinical Question

The trial also posted secondary outcomes for fatigue, sleepiness, and HVLT-IR, measured 4 weeks after radiotherapy. Those outcomes address symptoms and recall, whereas retention indicates whether participants completed the scheduled questionnaires. The distinction matters: a difference in questionnaire completion does not by itself establish a difference in fatigue, sleepiness, or recall. The registry record names the study as a feasibility study of armodafinil for brain radiation-induced fatigue, but a more detailed account of the study's intended feasibility criteria is not reported in the registry record.

3. Trial Design

The registry record describes a randomized, quadruple-masked, parallel phase 2 study comparing armodafinil with placebo. It lists Wake Forest University Health Sciences as sponsor, enrollment of 54, and a completed status. The recorded study start was 2010-08-01, with primary completion on 2013-01-08. These record details describe the trial's administrative design and timing; they do not explain how randomization was generated or how masking was implemented.

Both groups followed a matching oral once-daily schedule during brain radiotherapy and the subsequent stated treatment period. Armodafinil and placebo began no later than the fifth fraction of radiotherapy and continued for 9-11 weeks in the absence of unacceptable toxicity. The record labels the study quadruple-masked, but the identities of the masked parties and the procedures used to preserve masking are not reported in the registry record.

The primary endpoint was assessed among all randomized participants. The registry defines retention as completion of questionnaires at 4 weeks post-RT, with that visit also described as approximately 3 months post randomization. Secondary fatigue, sleepiness, and HVLT-IR results are posted for 4 weeks post-RT. The outcome descriptions do not give the instruments' full scoring rules or explain the direction of better scores, so scale values should be interpreted as reported rather than assigned a clinical meaning beyond their stated units.

Random assignment and a parallel-group comparison allow the posted group results to be read as a comparison between assigned strategies. However, the registry record does not report the allocation ratio, the randomization sequence method, the intended original sample size, or the rationale for the enrollment target. It also does not report a detailed protocol or statistical analysis plan. Those omissions limit assessment of how the executed trial matched its initial design.

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:

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

5. Baseline Characteristics

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

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Retention, measured over 4 weeks post-RT (approximately 3 months post randomization).

The primary endpoint, retention, is the percentage of participants who completed the questionnaires 4 weeks after radiotherapy. The registry also places this time point at approximately 3 months after randomization. Its stated population is all randomized participants. The outcome therefore describes completion of follow-up questionnaires, not the magnitude of fatigue or another symptom.

Retention is useful in a feasibility study because it gives information about whether participants contribute outcome data at the planned assessment. Questionnaire completion can affect how much information is available for evaluating patient-reported outcomes. A retention result is therefore relevant to the practicality of collecting those outcomes in this treatment setting. It does not establish why participants did or did not complete questionnaires, and the record does not give reasons for noncompletion.

The posted results list retention of 85.0% in the armodafinil arm and 75.0% in the placebo arm. The comparison summary also gives an unadjusted risk difference and its interval, discussed in the statistical interpretation. These values describe the registry's posted endpoint results. They should not be read as direct evidence of a change in fatigue, because completion and symptom level are different outcomes. The registry record does not report a prespecified threshold for acceptable retention or a criterion defining feasibility as successful.

7. Results Posted in the Registry

• Arm I - Armodafinil: 84.6% (22/26) versus 75.0% (21/28) on control; risk difference 9.6 percentage points (95% CI -11.6 to 30.8), risk ratio 1.13 (0.86–1.48); unadjusted two-proportion z-test p = 0.381.

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.

Fatigue

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Arm I - Armodafinil: mean 32.40 versus 36.40 on control; difference -4.00 (95% CI -11.07 to 3.07), standardized effect d = -0.30; z-test p = 0.267.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I - Armodafinil and the control. The interval gives the range of effects that remain compatible with the data.

Sleepiness

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Arm I - Armodafinil: mean 7.20 versus 8.30 on control; difference -1.10 (95% CI -3.87 to 1.67), standardized effect d = -0.21; z-test p = 0.437.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I - Armodafinil and the control. The interval gives the range of effects that remain compatible with the data.

HVLT-IR

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Arm I - Armodafinil: mean 21.20 versus 20.00 on control; difference 1.20 (95% CI -2.82 to 5.22), standardized effect d = 0.16; z-test p = 0.559.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I - Armodafinil and the control. The interval gives the range of effects that remain compatible with the data.

Across fatigue, sleepiness, and HVLT-IR, the posted point estimates favor different directions: the fatigue and sleepiness means are lower in the armodafinil group, while the HVLT-IR mean is higher. The intervals for all three mean differences include no difference, and their unadjusted p-values do not provide strong evidence against a no-difference model. Taken together, the secondary summaries do not establish a consistent, precise pattern across symptoms and recall.

These outcomes complement the primary retention result but answer different questions. Retention concerns whether questionnaires were completed; the secondary outcomes concern scores among the participants included in those analyses. A higher questionnaire completion proportion would not itself imply better symptom scores, and symptom-score comparisons do not explain why some questionnaires were not completed. The record does not report whether the secondary analyses used the same analysis population or how missing assessments were handled.

Unadjusted secondary results carry less weight because several outcomes were considered and the record does not report a multiplicity strategy. When multiple comparisons are examined, the chance of finding an apparently notable result by chance can increase. Adjustment methods or a prespecified hierarchy can address this concern, but neither is reported in the registry record. The registry also lists no reported secondary analyses, so the displayed comparisons are recalculations from posted summary statistics rather than documented sponsor analyses.

Interpretation is further limited by the absence of scale ranges, scoring direction details, clinically important thresholds, and model specifications. The posted means and intervals can be described in their recorded units, but they do not by themselves establish whether a difference would be meaningful to participants. The secondary outcomes are best viewed as exploratory context for the primary feasibility result, not as independent confirmation of a treatment effect.

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

• Fatigue
• Sleepiness
• HVLT-IR

9. Statistical Interpretation

10. Statistical Methods Explained

The trial uses a randomized parallel-group design: participants were assigned to armodafinil or placebo, and the groups were followed on the same general schedule. Randomization is intended to make assigned groups comparable in expectation, reducing systematic differences in measured and unmeasured characteristics. It does not guarantee balance in every realized study, particularly when the amount of information is limited. The registry record identifies randomization and quadruple masking but does not report the sequence-generation procedure, allocation concealment method, or which parties were masked.

What does the primary comparison estimate?

Retention is a binary outcome for each participant: questionnaire completion or noncompletion. A risk, or proportion, summarizes the frequency of the event in a group. The primary comparison is expressed as a risk difference, which subtracts the placebo group's proportion from the armodafinil group's proportion. A positive estimate means the observed proportion was higher in the armodafinil group; a negative estimate would mean it was higher in the placebo group. Unlike a relative measure, a risk difference remains on the absolute probability scale and can be interpreted in relation to the outcome's frequency. The record gives group percentages and an unadjusted comparison estimate.

The comparison summary also lists a p-value. In general, a p-value measures how unusual results at least as incompatible with a specified null model would be if that model and the analysis assumptions were true. It is not the probability that the null model is true, and it does not describe the size or practical importance of an effect. An unadjusted p-value has not been modified to account for testing multiple outcomes or comparisons. The registry record does not report a multiplicity adjustment.

How should a confidence interval be read?

In general, a confidence interval expresses the uncertainty around an estimated effect under a statistical model and its assumptions. A narrower interval indicates greater precision; a wider interval indicates less precision. When an interval for a difference includes no difference, the data are compatible with effects in either direction as well as with little or no difference. This does not prove equivalence. An equivalence conclusion would require a prespecified margin and an analysis designed for that question, neither of which is reported in the registry record.

For the primary risk difference, the posted interval extends from -0.116 to 0.308. Its breadth signals substantial uncertainty about the magnitude and direction of the retention contrast. The secondary mean-difference intervals also span no difference. Those intervals should be read in the units of their respective scales, not as probabilities. The record provides no clinically important thresholds with which to judge whether particular values within these intervals would matter to patients or researchers.

What do the secondary means represent?

The secondary outcomes are posted as least-squares means with standard errors. A least-squares mean is an estimate of a group mean from a statistical model; it can account for model terms when those terms are specified. The model specification and covariates are not reported in the registry record, so the adjusted basis of these posted means cannot be fully assessed. The standard error describes uncertainty in an estimated mean, not the spread of individual participants' scores. It should not be read as a standard deviation.

The recalculated mean differences and confidence intervals are simple, unadjusted comparisons based on the posted summary statistics. The pooled standard deviations used for planning are marked as approximate in the statistical summaries. Recalculated comparisons need not match a sponsor's model-based analysis if that analysis used covariate adjustment, repeated measurements, a different analysis population, or other methods. In this record, no sponsor-reported secondary analyses are listed. The primary comparison has no flagged discrepancy, so the posted comparison summary is the available basis for describing it.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model's assumed variability. If a model treats outcomes as less variable than they are, standard errors may be too small and intervals too narrow, making estimates appear more precise than warranted. If variability is modeled appropriately, uncertainty measures better reflect the data. Over-dispersion is especially relevant when outcomes are counts or clustered observations; the registry's primary retention outcome is binary, and it does not report an over-dispersion analysis. This general concept should not be taken as a claim that over-dispersion affected this trial.

What can planning calculations show?

Planning illustrations translate an assumed effect and statistical design into the approximate participants per arm required to achieve a chosen power target under stated assumptions. The posted illustrations use the observed effect and show alternatives based on detecting 75% or 50% of that effect. Smaller target effects generally require more participants because they are harder to distinguish from random variation. These calculations are not evidence that the original trial was designed using those assumptions. The trial's own original sample-size justification and statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary retention estimate is 0.096 on the risk-difference scale, with a confidence interval from -0.116 to 0.308. The interval covers values on both sides of no difference, so the posted evidence is compatible with higher retention in either group. Its width indicates that the result does not estimate the between-group contrast precisely. The point estimate alone should not be treated as the likely effect without considering that uncertainty.

A confidence interval is not a range guaranteed to contain the true effect. In general, it is a procedure that, under its assumptions, would capture the target parameter at its stated confidence level over repeated applications. The confidence level for this interval is not stated in the primary comparison details, so it is not reported in the registry record. Regardless of its nominal level, the interval's span is important: it accommodates both an unfavorable direction and a potentially favorable direction for the armodafinil group.

The posted secondary confidence intervals also cross no mean difference: fatigue ranges from -11.07 to 3.069, sleepiness from -3.872 to 1.672, and HVLT-IR from -2.822 to 5.222. Their scales differ, so widths should not be compared across outcomes as if they had a common unit. The registry does not report thresholds for clinically meaningful change, and the intervals therefore cannot be classified as excluding or including effects of a specified clinical importance.

Precision depends on the information available, variability, outcome frequency, and analysis method. The registry record does not supply enough detail to assess all contributors, including missing-data handling and model specification. A nonsignificant p-value does not mean the estimate is precise or that the groups are equivalent; the interval is the more direct description of the range of effects compatible with the posted summary under its assumptions.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes or total event counts. The calculations are planning illustrations based on the observed effect, not the original trial's design. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

In general, power is the probability that a planned study will detect an effect of the specified size under the assumed model and design. The 80% power column describes the participant requirement under a design intended to detect the chosen effect with 80% power; the 90% power column uses a higher target probability of detection and therefore has larger planning figures. These percentages describe design characteristics, not the probability that the result is true. This is not observed power.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the planning requirements change when the assumed target effect is reduced. Across the posted outcomes, the participant requirements rise for smaller target effects. This is expected: smaller differences are harder to distinguish from random variation, so more information is generally needed to detect them with the same power target. The illustrations should be read as conditional on the stated effect and assumptions, not as evidence that a future study will achieve a particular result.

The displayed calculations are separate for each outcome. They do not account for an unreported multiplicity plan, missing-data strategy, or adjustment for the actual analysis model. The posted planning assumptions identify equal allocation and a normal approximation, but do not establish that these were used for the trial's original design.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.750; treatment proportion p₁ = 0.846; average p̄ = 0.798.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5677 = 1.1127.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5636 = 0.4744.
4. n = (1.1127 + 0.4744)² / (0.0962)² = 272.4, rounded up to 273 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
p0 <- 0.75                          # control proportion
p1 <- 0.846153846153846                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1032200)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 273 (80% power), 365 (90% power)
 75% of observed effect: n per arm = 507 (80% power), 678 (90% power)
 50% of observed effect: n per arm = 1,187 (80% power), 1,589 (90% power)
power.prop.test: 272.4 
Simulated power at n = 273 per arm: 0.810 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists fatigue, sleepiness, and HVLT-IR as secondary outcomes, alongside the primary retention outcome. It does not report a prespecified hierarchy among these outcomes, a family of primary comparisons, or an adjustment for multiple testing. Without such information, unadjusted p-values for secondary comparisons should be interpreted cautiously. Considering several outcomes can make chance findings more likely, and a nominal p-value does not account for that broader testing context.

The record gives all randomized participants as the primary endpoint population, but does not describe how missing questionnaires were handled in the analysis. Retention is itself based on questionnaire completion, yet the reasons for noncompletion and any procedures for incomplete forms are not reported in the registry record. For the secondary endpoints, the posted arm-specific counts differ from the primary arm counts, but the record does not explain the analysis population, missingness, or exclusions. It is not possible to infer whether data were missing at random or whether a particular imputation method was used.

The registry does not report the statistical model for the least-squares means, covariate adjustments, analysis sets for the secondary outcomes, or a detailed statistical analysis plan. It also does not report interim analyses, stopping rules, or a sample-size justification for the original design. These omissions prevent a full appraisal of whether the reported comparisons followed prespecified methods or how the analysis addressed missing data and multiple outcomes.

The absence of these details does not demonstrate that the trial lacked such procedures; it means they are not reported in the registry record. For interpretation, the safest distinction is between the stated primary endpoint definition and the available posted summaries, on one hand, and undocumented analysis choices, on the other. The posted unadjusted comparisons should not be read as if they were necessarily the complete prespecified analysis.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: headache (7.7%), agitation (7.4%), infections and infestations - other (7.4%), nausea (7.4%), anemia (3.8%).

The registry reports serious adverse events affecting 10 participants in the armodafinil group, with 26 at risk, and 8 participants in the placebo group, with 27 at risk. It separately reports other adverse events affecting 26 participants at risk in the armodafinil group and 27 participants at risk in the placebo group. Deaths recorded were 1 and 2, respectively. These are registry counts, not a causal assessment of whether an event was caused by study treatment.

The listed serious adverse event terms and percentages include headache (7.7%), agitation (7.4%), infections and infestations - other (7.4%), nausea (7.4%), anemia (3.8%), and anxiety (3.8%). The record does not provide enough detail in these summaries to determine event timing, severity grading, recurrence, attribution, or whether individuals experienced more than one event. Serious adverse events and other adverse events are separate reporting categories and should not be conflated.

These figures describe reported safety events within the recorded groups. They do not by themselves establish comparative risk or causation, and should be interpreted alongside the limited study size and the registry's level of detail.

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

The registry's primary results describe questionnaire retention at 4 weeks after radiotherapy: 85.0% in the armodafinil group and 75.0% in the placebo group. The estimated risk difference is 0.096, but its confidence interval extends from -0.116 to 0.308. That uncertainty means the posted result does not establish a precise difference in retention or rule out effects in either direction.

Retention is a feasibility-related measure, not a direct measure of fatigue relief. The trial's name and rationale concern fatigue associated with brain radiation, and fatigue was also posted as a secondary outcome. However, neither the primary retention percentage nor completion of questionnaires alone establishes how participants felt. The fatigue comparison is uncertain, and the registry does not report a clinically important threshold for interpreting its scale. The same caution applies to sleepiness and HVLT-IR.

These results do not prove that the groups are equivalent. A failure to show a clear difference is not the same as evidence that any difference is negligibly small. Demonstrating equivalence or noninferiority would require a defined margin and an analysis designed for that purpose; those are not reported in the registry record. Nor do the posted summary comparisons establish that the intervention caused any observed difference, particularly without fuller information about analyses and missing data.

The study is described as completed and as a feasibility study, but the registry does not report a threshold for success or the original sample-size rationale. The numerical results can therefore be interpreted as estimates with substantial uncertainty, rather than as a definitive decision about feasibility or clinical effect. They offer a record of the measured outcomes in the groups, with important limits on how far those observations can be generalized.

17. Why This Trial Matters Statistically

This trial illustrates why a feasibility outcome and a clinical outcome need to be kept distinct. Retention assesses whether participants completed questionnaires at the planned follow-up; it helps characterize the availability of patient-reported data. It does not stand in for fatigue severity. The separate fatigue, sleepiness, and recall results address different constructs, and each has its own uncertainty and interpretation.

It also illustrates the value of intervals alongside point estimates. The observed retention percentages differ descriptively, but the risk-difference interval allows a broad range of possible comparisons. A point estimate can be visually compelling while remaining imprecise. Statistical interpretation should therefore consider both the direction of the estimate and how much uncertainty surrounds it, rather than treating a single p-value as a complete verdict.

The registry's planning illustrations show how sample requirements depend on the effect a study aims to detect. A design targeting a smaller effect generally needs more participants than one targeting the full observed effect. This makes clear why a small completed study may offer limited precision even when a point estimate appears substantial. The planning figures are illustrations, not a reconstruction of the original design.

Finally, the record demonstrates the importance of transparent reporting. Information about missing data, analysis populations, multiplicity, model specifications, and the original sample-size justification would help readers assess how the posted estimates were produced and how robustly they answer the study question. Their absence in the registry record should be treated as uncertainty about documentation, not proof that the procedures did not exist.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations specific to this record affect interpretation. The enrollment is reported as 54, but the primary comparison remains imprecise, as reflected by its broad confidence interval. The registry does not report the original sample-size justification or the feasibility threshold that would define an acceptable retention result. Thus, the enrollment cannot be evaluated against a documented target, and the observed retention cannot be classified against a stated success criterion.

Details needed to assess the analysis are not reported in the registry record: the randomization procedure, allocation concealment, masked roles, analysis model, covariate adjustment, missing-data handling, and analysis populations for secondary outcomes. The secondary summaries have no reported sponsor analyses, and the comparisons are unadjusted recalculations from posted summary statistics. This limits confidence that they represent the full planned analyses.

The record also does not report scale ranges, score direction for every instrument, clinically important differences, or reasons for questionnaire noncompletion. Without these details, scale estimates are difficult to translate into clinical meaning, and retention differences cannot be explained. No multiplicity strategy is reported despite several outcomes, which makes the secondary p-values exploratory.

Safety summaries provide counts and selected serious event terms, but not detailed attribution, timing, grading, or recurrence. Finally, the registry description alone does not establish generalizability beyond the stated setting of patients with primary brain tumors receiving brain radiotherapy. These are limitations of what is documented; they should not be read as proof that additional methods or information were unavailable elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Armodafinil in Treating Fatigue Caused By Radiation Therapy in Patients With Primary Brain Tumors — NCT01032200.
• Registry record last updated 2021-09-28; status last verified 2021-09.
• Results first posted 2017-02-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized, quadruple-masked, parallel phase 2 trial comparing once-daily oral armodafinil with placebo during brain radiotherapy and for 9-11 weeks, absent unacceptable toxicity. The primary outcome was questionnaire retention 4 weeks post-RT, approximately 3 months after randomization, among all randomized participants.

Retention was reported as 85.0% for armodafinil and 75.0% for placebo. The posted risk-difference interval includes no difference and leaves substantial uncertainty about the comparison. Secondary summaries for fatigue, sleepiness, and HVLT-IR are also uncertain and lack reported sponsor analyses. The registry does not report the original sample-size rationale, missing-data methods, or multiplicity plan. These results describe the posted data but do not establish a precise clinical effect.