Flumazenil for the Treatment of Primary Hypersomnia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Flumazenil for the Treatment of Primary Hypersomnia (NCT01183312), a randomized phase 1, phase 2 study. The primary outcome is Change in Psychomotor Vigilance Task (PVT) Median Reaction Time.

2. Clinical Question

The clinical question concerns a short-term, measured response to a single day of dosing, not sustained effects over longer treatment. The primary outcome averages measurements taken at several post-administration times into one on-treatment value for each participant. That approach produces one summary per treatment period, rather than treating each time point as a separate primary result.

The registry background describes a proposed mechanism involving excess endogenous potentiation of GABA-A receptors in a subset of people with hypersomnia. The trial title also narrows the study population to people with this characteristic or excessively long total sleep time. The registry record does not report further eligibility thresholds or how the proposed receptor characteristic was assessed.

The question is comparative: the relevant evidence is the difference between the flumazenil and placebo conditions, not whether either condition's average change alone is positive or negative. Because the trial uses a crossover, each sequence receives both conditions; this makes within-participant comparison relevant to the design. The posted primary comparison does not establish whether any effect would persist beyond the assessment period.

3. Trial Design

This was a randomized, quadruple-masked, crossover study listed in phases 1 and 2. Enrollment was 10, and the status is completed. The registry records a study start of 2010-09 and primary completion of 2012-01. The sponsor is listed as Lynn Marie Trotti.

Participants were assigned to one of two treatment sequences. One sequence received a day of placebo followed by a day of sublingual flumazenil; the other received flumazenil followed by placebo. Thus, the design intended for participants to experience both study conditions in different orders. The registry record does not report a washout interval, how treatment order was generated, or whether period and sequence effects were considered in the statistical analysis.

Masking is recorded as quadruple. The registry does not specify which groups of people were masked or how masking was maintained. No dose amount is reported in the registry record. The dosing description is limited to single-day sublingual administration in the title and arm descriptions.

The primary population is described as intention to treat, with all randomized subjects included. Both treatment arms list 10 participants for the primary endpoint. The primary completion date and completed status identify a finished study, but do not establish that every planned analysis or assessment was reported.

The registry record does not report the original sample-size justification, a formal protocol-based power target, the planned handling of crossover carryover or period effects, or an interim-analysis plan. It also does not report whether there were protocol amendments. Those omissions limit how fully the published results can be connected to the trial's original design choices.

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: 12 patients were enrolled; of these, 2 were excluded prior to randomization because screening laboratory test results were abnormal.

First Intervention Day

Washout Period of at Least 1 Week

Second Intervention Day

Analysis population for the primary outcome, as defined in the registry: Intention to treat (all randomized subjects were included)

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change in Psychomotor Vigilance Task (PVT) Median Reaction Time, measured over 10, 30, 60, 90, 120, and 150 minutes after drug administration (averaged for all time points for each subject).

The primary endpoint is change in median reaction time on the psychomotor vigilance task, reported in msec. During the task, a participant responds to a visual stimulus by pressing a button. The recorded reaction-time measure is the median across multiple presentations during the 10 minute task.

For each participant, the primary outcome compares baseline with the treatment-period value. The registry defines the change as baseline value minus treatment value, so a higher number represents improvement from baseline under that definition. Measurements after drug administration were taken at 10, 30, 60, 90, 120, and 150 minutes. The values at those time points were averaged to create one on-treatment value for each participant.

Vigilance tasks are used to quantify alertness-related performance in a structured way. In this trial, reaction time provides a continuous measure rather than a simple yes-or-no outcome. The median can summarize typical performance while being less dominated by unusually long or short responses than an arithmetic average of all responses would be. That is a general feature of medians; the registry does not report why this particular summary was selected.

The endpoint is a task-based measure over a short post-dose period. It is not itself a direct measure of daily functioning, long-term sleepiness, or sustained treatment response. The registry does not report a threshold for a clinically important change in reaction time, so the statistical difference cannot be translated into a stated clinical-importance category from this record alone.

7. Results Posted in the Registry

• Sublingual Flumazenil: mean -4.46 versus -9.86 on control; difference 5.40 (95% CI -37.78 to 48.58), standardized effect d = 0.11; z-test p = 0.806.

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.

PVT Additional Measure #1, Change in Lapse Frequency

• 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 deviations.
• Result:
  • Sublingual Flumazenil: mean -2.60 versus -3.30 on control; difference 0.70 (95% CI -6.18 to 7.58), standardized effect d = 0.09; z-test p = 0.842.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sublingual Flumazenil and the control. The interval gives the range of effects that remain compatible with the data.

PVT Additional Measure #2, Change in Duration of Lapse Domain

• 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 deviations.
• Result:
  • Sublingual Flumazenil: mean 0.25 versus 0.18 on control; difference 0.07 (95% CI -0.27 to 0.41), standardized effect d = 0.18; z-test p = 0.682.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sublingual Flumazenil and the control. The interval gives the range of effects that remain compatible with the data.

PVT Additional Measure #3, Change in Optimum Response Times

• 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 deviations.
• Result:
  • Sublingual Flumazenil: mean -0.04 versus -0.02 on control; difference -0.02 (95% CI -0.44 to 0.40), standardized effect d = -0.04; z-test p = 0.926.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sublingual Flumazenil and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of performance during psychomotor vigilance testing, subjective sleepiness, and electroencephalogram power. The posted results include additional PVT measures, a Stanford Sleepiness Scale measure, and EEG power. These outcomes broaden the assessment beyond median reaction time, but they do not replace the designated primary endpoint.

Across the secondary endpoints with numerical results posted, the recalculated mean differences are small relative to their uncertainty, and their confidence intervals include zero. The sponsor-reported paired tests also do not provide strong evidence of differences on the listed secondary measures. Taken together, this pattern is broadly consistent with the uncertain primary comparison rather than providing a clear, consistent signal across the measured outcomes.

Secondary endpoints can be useful for understanding whether an intervention's observed pattern is consistent across different measurements. They can also be exploratory, especially in a small study. The registry does not report a hierarchy of secondary hypotheses or a multiplicity adjustment. When multiple outcomes are tested, unadjusted p-values should be treated cautiously because repeated testing can produce apparently notable results by chance. A secondary result should not be elevated to a definitive conclusion simply because it is statistically unusual.

The results are not all presented with the same level of detail: the registry reports paired-test p-values, while the recalculated comparisons use summary statistics. The absence of participant-level paired estimates and confidence intervals limits how precisely the secondary effects can be compared across measures. The registry record also does not report a clinical-importance threshold for these outcomes. Accordingly, the secondary pattern is best viewed as additional descriptive evidence, with the primary result and the trial's limited size kept in view.

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

• PVT Additional Measure #1, Change in Lapse Frequency
• PVT Additional Measure #2, Change in Duration of Lapse Domain
• PVT Additional Measure #3, Change in Optimum Response Times
• PVT Additional Measure #4, Change in False Response Frequency
• PVT Additional Measure #5, Change in Visual Analog Scale Rating of Sleepiness at the Completion of PVT
• Change in Stanford Sleepiness Scale
• Electroencephalogram (EEG) Power

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is continuous: each participant has a numerical change in reaction time. The registry reports the arm values as means and standard deviations. A mean describes the arithmetic average, while a standard deviation describes the spread of participant values around that average. In general, a larger standard deviation indicates more variability in the observed responses. These summaries describe the data but do not by themselves account for the crossover pairing.

What does a paired test do?

The sponsor-reported primary analysis is a Wilcoxon signed-rank test, marked as paired. In general, a paired method evaluates within-participant differences between two conditions. This is appropriate to consider for a crossover structure because each participant receives both conditions, and the participant can serve as their own comparison. The signed-rank procedure ranks the sizes of nonzero paired differences and uses their directions to assess whether the differences tend to be centered around zero. It does not require the paired differences to follow a normal distribution in the way a conventional paired t-test does, although it has its own assumptions about the distribution of differences.

The sponsor's reported result is p = 0.77. The registry does not give the test statistic, a paired effect estimate, or a confidence interval for this analysis. A p-value summarizes how compatible the observed data are with the test's null hypothesis under the assumptions of that test. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate.

What does the recalculated comparison represent?

The recalculated mean difference is based on the posted arm-level summary statistics. It is a simple unadjusted comparison, with flumazenil compared against placebo. It gives a mean difference of 5.4 msec and a 95% confidence interval from -37.78 to 48.58, with p = 0.806. This is not the same analysis as the sponsor's paired Wilcoxon test: the recalculation uses the available group summaries, while the reported test uses paired participant-level differences. The recalculated comparison is therefore a supplementary description, not a substitute for the crossover analysis.

In general, paired and unpaired analyses can differ because they use different information about how each person's responses relate across conditions. The extent of that relationship is not available in the registry summaries. The recalculated standard error and interval consequently should not be mistaken for a paired confidence interval or for the sponsor's reported analysis.

Why consider the confidence interval alongside the p-value?

A confidence interval describes a range of effect sizes compatible with the data and the method used to calculate it. In general, a narrow interval implies more precision, while a wide interval leaves more uncertainty. The primary interval extends from -37.78 to 48.58 msec and crosses zero. That span conveys that the recalculated data are compatible with a range of comparative effects rather than pinpointing a precise difference.

The p-value and interval answer related but different questions. A p-value summarizes evidence against a specified null value, while an interval communicates both direction and a range of plausible effect sizes. Neither establishes clinical importance by itself. The record does not supply a threshold that would identify a clinically important change on this task.

How should the crossover structure be considered?

A crossover assigns participants to treatment sequences and observes each participant under both conditions. This can reduce the influence of stable differences between people when the analysis compares each person with themself. It also makes order and timing relevant: treatment effects could be affected by period, sequence, or carryover. The registry record does not report the washout interval or the planned statistical handling of these issues. The paired sponsor analysis acknowledges the within-person comparison, but its reported p-value alone does not show how period or carryover effects were assessed.

The primary outcome is designated intention to treat, and the registry says all randomized subjects were included. That identifies the stated analysis population. It does not fully describe missing-data procedures, deviations from assigned sequence, or how incomplete outcome measurements would have been handled. These details are not reported in the registry record.

For the additional outcomes, the registry reports paired Wilcoxon signed-rank tests. Those tests concern secondary measures and should be interpreted in the context of multiple outcomes. The registry does not report a multiplicity adjustment or a pre-specified hierarchy for testing them. In general, when many outcomes are tested, the chance of at least one apparently unusual result can increase, so isolated unadjusted findings deserve caution.

11. Confidence Intervals and Precision

The recalculated primary estimate is a mean difference of 5.4 msec, and its 95% confidence interval runs from -37.78 to 48.58. The interval is broad relative to the point estimate and includes zero. It therefore indicates limited precision: the observed data do not tightly locate the comparative effect.

In general, a confidence interval is a range constructed by a statistical procedure that, across repeated samples under its assumptions, would contain the target quantity at the stated frequency. A 95% interval is not a statement that there is a 95% probability that this particular fixed effect lies inside these particular limits. The interpretation also depends on the analysis method and its assumptions.

The interval accompanies a simple unadjusted recalculation from posted summaries. The sponsor reported a paired Wilcoxon test, but no paired effect estimate or confidence interval is reported in the registry record. The recalculated interval should therefore not be attributed to the sponsor's paired analysis or treated as the interval from a crossover-adjusted model.

The interval covers negative and positive differences, so the data are compatible with effects in either direction under this calculation. Its width reflects substantial uncertainty, consistent with the small study enrollment and variability in the participant-level results. The interval does not establish that all values within it are equally plausible, nor does it define which values would matter clinically.

Because the registry does not provide a clinically important difference threshold, precision can be described statistically but not classified against a stated clinical benchmark. The record also does not report a confidence interval for the paired sponsor analysis. That missing estimate limits direct assessment of precision under the analysis that accounts for the within-participant comparison.

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 estimates express the number of participants per arm, not a total event count. The estimates are illustrations based on the observed effect and are not the original trial's design calculation. The original sample-size justification and its assumptions are not reported in the registry record.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For each scenario, the effect to detect is set to the stated fraction of the observed effect. The rows therefore consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects require more participants because a subtler difference is harder to distinguish from random variation.

The 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column gives the corresponding estimate for a design with a 90% chance. Higher power generally requires more participants, all else equal. These are planning targets, not descriptions of the trial's achieved ability to find an effect.

The estimates are based on an observed effect from a very small crossover study, while the planning assumptions describe equal allocation between two arms. They should be read as simplified illustrations rather than as a design recommendation for a future crossover study. A new design would need assumptions suited to its population, outcome, analysis, and treatment sequence. These values are 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 = 5.400; pooled standard deviation σ = 49.259.
2. n = 2 × (1.96 + 0.842)² × 49.259² / 5.400² = 1,306.2, rounded up to 1,307 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 <- 5.4                      # observed difference in means
sigma <- 49.25916158442                     # 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(1183312)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,307 (80% power), 1,749 (90% power)
 75% of observed effect: n per arm = 2,323 (80% power), 3,109 (90% power)
 50% of observed effect: n per arm = 5,225 (80% power), 6,995 (90% power)
power.t.test: 1307.2 
Simulated power at n = 1,307 per arm: 0.798 (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 reports the sponsor's primary analysis as a paired Wilcoxon signed-rank test with p = 0.77. It does not report a paired effect estimate or confidence interval for that test. The recalculated comparison uses arm-level means and standard deviations, yielding a mean difference of 5.4 msec, a 95% confidence interval from -37.78 to 48.58, and p = 0.806.

The two p-values are not identical because the analyses differ: one is a paired rank-based test, and the other is an unadjusted recalculation from posted summary statistics. The recalculated comparison does not recover the participant-level pairing used by the sponsor's test. Its interval is consequently not an interval for the sponsor's paired estimate.

No discrepancy is flagged between the posted outcome and the recalculated summary. The sponsor's paired result remains the registry-reported analysis, while the recalculation offers a separate, transparent comparison of the posted arm summaries. Both results indicate that the reported analysis does not provide strong evidence of a difference, but neither establishes equivalence or rules out effects that could matter. The absence of a paired estimate and interval makes the magnitude and precision under the sponsor's method harder to assess.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and multiple secondary outcomes, including several measures related to the psychomotor vigilance task. Testing multiple outcomes raises a multiplicity issue: in general, the more hypotheses tested, the greater the chance that at least one result appears unusual even when there is no true effect. This is why secondary p-values are commonly interpreted in relation to a pre-specified testing hierarchy or an adjustment procedure.

The registry record does not report whether the trial used a multiplicity adjustment, a gatekeeping strategy, or a formal ordering of secondary hypotheses. It does not report an interim-analysis plan or stopping boundaries. Without those details, the reported secondary p-values should be understood as unadjusted results unless otherwise stated in the record; the statistical plan for multiplicity is not reported in the registry record.

The primary population is described as intention to treat, with all randomized subjects included. This identifies the intended analysis population but does not explain how missing observations, missed assessments, or departures from assigned treatment sequence were handled. The registry does not report the number of missing primary measurements or a missing-data method. The equal counts listed for treatment conditions do not establish that every measurement at every time point was complete.

For a crossover study, interpretation can also depend on the sequence and period structure. The record describes the two orders of treatment but does not report how period effects, carryover, or sequence effects were modeled or assessed. It also does not report a washout interval. Those are design and analysis details that would help readers understand whether the within-person comparison adequately reflects the treatment contrast.

The primary result should therefore be read alongside the uncertainty in the estimate and the limited detail about analysis planning. The registry record does not report enough information to determine how the missing-data, multiplicity, and crossover-specific issues were addressed beyond the named paired test and the intention-to-treat population description.

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 non-serious adverse event terms

The registry reports zero participants with a serious adverse event in each condition: 0 of 10 for placebo and 0 of 10 for sublingual flumazenil. No serious adverse-event terms are listed. This means that no serious events are recorded in these groups in the registry results; it does not establish that the risk of serious events is absent, particularly given the small number of participants.

The registry also lists other adverse events affecting 4 participants during placebo and 9 during sublingual flumazenil, with 10 at risk in each condition. These counts are separate from the serious-event figures. The record does not provide event-level detail in the listed safety summary, so the counts alone do not convey severity, duration, relationship to treatment, or whether a participant experienced more than one event.

Deaths are not reported in the registry record. The safety figures should be interpreted as counts observed in this small study, not as precise estimates of comparative safety or as a basis for conclusions about uncommon events.

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

The primary result estimates a short-term difference in change in median reaction time between a day of sublingual flumazenil and a day of placebo. The recalculated mean difference is 5.4 msec, and the 95% confidence interval ranges from -37.78 to 48.58. The sponsor-reported paired test has p = 0.77. Together, these data do not provide strong statistical evidence of a difference, while the interval leaves considerable uncertainty about the size and direction of the effect.

This is not evidence that the two conditions are equivalent. Equivalence requires a pre-specified margin defining differences small enough to count as practically similar, together with an analysis designed to evaluate that margin. No such margin is reported. Nor does the result prove that there is no effect: a wide interval can include both zero and effects in either direction.

The endpoint is a laboratory-style vigilance task averaged across post-dose measurements on a single day. The registry does not report that the result predicts long-term sleepiness, everyday functioning, or outcomes after longer exposure. It also does not report a threshold for a clinically important change. Statistical evidence about the measured outcome cannot be translated into a broader clinical conclusion that the record does not test.

The trial enrolled 10 participants and used a crossover design, so each participant was assigned to receive both study conditions in sequence. The design can support within-person comparison, but the registry gives limited detail about washout, period effects, and the analysis of these features. The sponsor's paired test is the reported analysis; the recalculated interval is an unadjusted summary-based comparison and should not be substituted for a paired estimate.

The results apply to this small study population and the specific dosing and assessment described in the registry. The record does not establish that findings generalize to all people with hypersomnia, to other treatment schedules, or to longer-term outcomes. The appropriate conclusion is limited: the posted data are imprecise and do not show a clear difference on the primary task measure, while leaving a wide range of possible effects unresolved.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it combines a crossover design with a small participant count and a continuous outcome. A crossover allows each participant to receive both conditions, making paired analysis a natural consideration. The registry does report a paired Wilcoxon test, but it does not provide the paired effect estimate or its confidence interval. Readers therefore see a test result without a directly reported estimate of the size and precision under that method.

The recalculated comparison demonstrates why the analysis method matters. Summary-based arm comparisons produce an estimate and interval, but do not preserve the participant-level pairing. Those quantities can help describe the posted means, yet they do not reproduce the sponsor's paired analysis. In general, reporting effect estimates and intervals from the planned analysis alongside test results helps readers understand both direction and precision.

The result also illustrates why a non-significant test is not the same as proof of no effect. The interval is broad and crosses zero, leaving substantial uncertainty. A small study can produce an estimate that is unstable, and a non-significant p-value cannot by itself distinguish a genuinely negligible effect from an imprecisely estimated one.

Finally, the registry includes several secondary measures, making interpretation of multiplicity relevant. The record does not report an adjustment or outcome hierarchy. This highlights the value of transparent statistical plans, complete estimates, and clear reporting of missing-data and crossover-specific decisions. These are general statistical lessons; they do not alter what was observed in this trial.

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.

The principal limitation is the small enrollment: 10 participants. That count constrains precision and limits the ability to characterize variation across participants. The primary confidence interval is broad, and the registry does not provide a paired estimate and interval for the sponsor-reported analysis.

The study evaluates single-day dosing and post-administration measurements through 150 minutes. The registry does not report longer-term follow-up results, so the posted outcomes do not address persistence of any response. The primary endpoint is a task measure, and the record does not provide a clinical-importance threshold for interpreting its magnitude.

The crossover structure makes treatment order and possible carryover relevant, but the registry record does not report the washout interval or how period, sequence, and carryover were handled analytically. The record also does not state which parties were masked despite listing quadruple masking, or how masking was implemented.

The registry describes the primary analysis population as intention to treat but does not report missing-data procedures, the completeness of all time-point measurements, or how protocol deviations were handled. The original sample-size justification, interim-analysis plan, multiplicity strategy, and detailed statistical plan are not reported in the registry record.

Finally, secondary outcomes are numerous, and the record does not report a multiplicity adjustment or a formal hierarchy. Their unadjusted tests offer supporting descriptive context but should not be treated as independent confirmation. These limitations concern precision, transparency, and scope; they do not by themselves determine the direction of any treatment effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Flumazenil for the Treatment of Primary Hypersomnia — NCT01183312.
• Registry record last updated 2017-12-12; status last verified 2017-11.
• Results first posted 2013-03-27.
• 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, quadruple-masked crossover study in phase 1 and phase 2, with enrollment of 10. Participants received placebo and sublingual flumazenil in one of two sequences. The primary endpoint was change in median psychomotor vigilance task reaction time, averaged across post-administration assessments.

The sponsor-reported paired Wilcoxon signed-rank test for the primary outcome has p = 0.77. A recalculated unadjusted mean difference is 5.4 msec, with a 95% confidence interval from -37.78 to 48.58. The estimate is imprecise and does not establish equivalence or rule out effects in either direction. Secondary results and safety counts provide additional context, but limitations include the small enrollment and unreported details about missing data, multiplicity, and crossover-specific analysis.