Rapid Determination Of The Clinical Utility Of Perampanel For The Treatment Of Alcohol Dependence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rapid Determination Of The Clinical Utility Of Perampanel For The Treatment Of Alcohol Dependence (NCT02120365), a randomized phase 1, phase 2 study. The primary outcome is Biphasic Alcohol Effects Scale (BAES): Stimulant Subscale.

2. Clinical Question

The study asked whether perampanel changes heavy drinkers’ response to alcohol in a laboratory setting. The registry describes the central hypothesis as a reduction in alcohol’s rewarding and reinforcing properties. The primary measure focused on stimulant effects during alcohol intoxication, rather than on treatment outcomes or drinking behavior outside the laboratory.

The crossover structure means participants experienced multiple conditions rather than belonging to a single treatment group throughout. The registry describes the laboratory test days as occurring in randomized order. The question is therefore about measured responses under these laboratory conditions, not about whether perampanel changes long-term alcohol use, dependence, or clinical outcomes. Those broader outcomes are not reported in the registry record.

3. Trial Design

The registry identifies this as a randomized, triple-masked crossover study in Phase 1 and Phase 2. It lists Virginia Commonwealth University as the sponsor, an enrollment of 22, and a completed status. The listed start date is 2019-06-01 and the primary completion date is 2022-02-15.

Participants were non-treatment-seeking heavy drinkers and took part in three separate laboratory days. The descriptions indicate that the test days followed different perampanel or placebo conditions and were scheduled in randomized order. Each session included a one-time alcohol infusion. For the perampanel conditions, the descriptions refer to daily perampanel 2mg pretreatment and an observed laboratory dose of 6mg or 10mg before the infusion. The placebo description also refers to pretreatment and an observed placebo dose. The arm descriptions contain incomplete timing text, so the full schedule and any washout arrangements are not reported in the registry record.

Because the design is crossover, each participant could contribute measurements under more than one condition. That structure can make within-person comparisons informative, but the statistical treatment of repeated observations depends on the specific model. The registry names a mixed models analysis but does not report the full model specification, including the terms used to represent participant, treatment, period, or sequence. The posted arm counts differ across conditions, and these counts should not be mistaken for independent groups of people in a parallel trial.

The registry lists a primary outcome and secondary measures of alcohol urge, side effects, and mood. It does not report the planned sample-size justification or the original assumptions used to design the trial. The posted analyses therefore describe the recorded results, while the design rationale and some details needed to assess the model cannot be reconstructed from the registry record.

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: random assignment. Crossover

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Non-treatment Seeking Heavy Drinkers of whom all participated in three separate lab days, each following a different dose of perampanel or placebo.

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: Non-treatment seeking heavy drinkers- This is a crossover design. Subjects each completed at least one of the three dosages for a lab day.

6. Primary Endpoint

The registry lists the primary outcome as Biphasic Alcohol Effects Scale (BAES): Stimulant Subscale, measured over 98 minutes.

The primary endpoint was the Biphasic Alcohol Effects Scale stimulant subscale, reported as a score on a scale at the 98 minutes timeframe. The scale has 14 items: 7 intended to assess stimulant effects from alcohol intoxication and 7 intended to assess sedative effects. The primary outcome uses the stimulant subscale, not the sedative subscale.

Each item can be scored from 0 to 10, with higher item scores representing feeling more or most intoxicated for that item. The stimulant subscale includes 7 items, and the full scale has a minimum score of 0 and a maximum of 70. For the reported timeframe, observations at different time points were combined by averaging values over the interval from 12 to 110 minutes. The resulting outcome is therefore a summary of the response during that interval, not a measurement at one isolated moment.

The registry says the scale was selected as a primary outcome because it is sensitive to alcohol’s effects. In this study, the endpoint makes the laboratory response measurable and allows comparison among placebo and the two perampanel-dose conditions. It does not directly measure alcohol consumption, dependence severity over time, or clinical benefit. The posted values are least-squares means with standard errors, and the sponsor reports a mixed models analysis. Full details of how that model handled the repeated laboratory observations are not reported in the registry record.

7. Results Posted in the Registry

• Perampanel 6mg Dose: mean 14.05 versus 13.76 on control; difference 0.30 (95% CI -7.19 to 7.79), standardized effect d = 0.03; z-test p = 0.938.
• Perampanel 10mg Dose: mean 13.03 versus 13.76 on control; difference -0.73 (95% CI -8.44 to 6.98), standardized effect d = -0.07; z-test p = 0.853.

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.

Alcohol Urge Questionnaire (AUQ)

• 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:
  • Perampanel 6mg Dose: mean 17.31 versus 16.48 on control; difference 0.83 (95% CI -2.56 to 4.22), standardized effect d = 0.17; z-test p = 0.630.
  • Perampanel 10mg Dose: mean 18.72 versus 16.48 on control; difference 2.24 (95% CI -1.30 to 5.78), standardized effect d = 0.46; z-test p = 0.215.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 6mg Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 10mg Dose and the control. The interval gives the range of effects that remain compatible with the data.

Side Effect Questionnaire (SEQ)

• 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:
  • Perampanel 6mg Dose: mean 0.99 versus 0.90 on control; difference 0.10 (95% CI -0.67 to 0.87), standardized effect d = 0.09; z-test p = 0.805.
  • Perampanel 10mg Dose: mean 1.13 versus 0.90 on control; difference 0.23 (95% CI -0.56 to 1.03), standardized effect d = 0.22; z-test p = 0.563.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 6mg Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 10mg Dose and the control. The interval gives the range of effects that remain compatible with the data.

Profile of Mood States (POMS) 2 Short Version Total Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Perampanel 6mg Dose: mean 21.75 versus 20.25 on control; difference 1.50 (95% CI -2.42 to 5.42), standardized effect d = 0.27; z-test p = 0.453.
  • Perampanel 10mg Dose: mean 20.62 versus 20.25 on control; difference 0.37 (95% CI -3.82 to 4.56), standardized effect d = 0.06; z-test p = 0.863.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 6mg Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Perampanel 10mg Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover alcohol urge, side effects, and mood. Across these measures, the posted summaries do not show a consistent pattern of separation between placebo and both perampanel conditions. Some point estimates are higher under a perampanel condition, while others are close to placebo, and the recalculated intervals generally leave considerable uncertainty about the size and direction of differences.

This broad pattern does not materially strengthen or overturn the primary-outcome interpretation. The secondary measures are related to the laboratory experience but represent different constructs from the BAES stimulant subscale. They may offer context about urge, reported side effects, and mood during the laboratory period, but they do not replace the prespecified primary endpoint or answer questions about longer-term alcohol use.

Unadjusted secondary results carry less weight when several outcomes and comparisons are considered. General statistical principle: the more tests performed, the greater the chance that one or more may appear notable by chance, even when there is no underlying effect. A multiplicity adjustment or a prespecified testing hierarchy can address this issue, but the registry does not report whether such a plan was used. The sponsor reports mixed-model analyses for the secondary measures, while the simple pairwise recalculations are unadjusted and approximate.

The overall secondary pattern should therefore be treated as exploratory context rather than a collection of independent confirmations. The registry lists three secondary outcomes and reports analyses for them, but does not describe a confirmatory strategy or explain how the family of outcomes was handled. In the absence of that information, isolated estimates or p-values should not be elevated over the primary finding.

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

• Alcohol Urge Questionnaire (AUQ)
• Side Effect Questionnaire (SEQ)
• Profile of Mood States (POMS) 2 Short Version Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports the primary endpoint as a least-squares mean with a standard error and names a mixed models analysis for the sponsor’s primary comparison. The posted summary results also support simple unadjusted comparisons between placebo and each perampanel dose. These analyses answer related but not identical questions, so their estimates and p-values should be kept distinct.

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group mean. It can differ from a raw arithmetic average because the model may account for other terms or features of the design. The registry identifies the reported values as least-squares means, but the specific model terms and estimation details are not reported in the registry record. The values should therefore be read as the model-based summaries posted for each condition, not as a complete description of the underlying analysis.

Why use a mixed model in a crossover study?

In a crossover study, observations from the same participant can be related. A mixed model can be used to represent that dependence while estimating condition differences, if the model is specified to reflect the design. The name of the method alone does not reveal which participant-level or design terms were included, how missing observations were treated, or how the sequence of conditions was handled. Those details are not reported in the registry record. This limits independent assessment of the model and prevents exact reconstruction from the posted group summaries.

The primary endpoint averages measurements across multiple time points within the stated interval. Repeated measurements over time may also be related to one another. Appropriate modeling can account for such dependence, but the registry does not describe the time structure or covariance assumptions used. General statistical principle: ignoring dependence among repeated observations can make standard errors and inferential results misleading. Whether and how that issue was addressed in the sponsor’s model cannot be determined from the posted description.

What do the recalculated contrasts show?

The recalculated values are simple, unadjusted mean differences between each perampanel condition and placebo. The 6mg estimate is 0.297, and the 10mg estimate is -0.73. The corresponding intervals and p-values are based on a reconstruction from the posted summary statistics, not a re-fit of the sponsor’s mixed model. The pooled standard deviations used in those calculations are approximate because they were inferred from the reported standard errors. The recalculations do not incorporate model terms or within-participant relationships that cannot be recovered from the summaries.

A mean difference expresses the estimated separation between two condition means on the original outcome scale. Its sign indicates the direction of the contrast as defined for the recalculation: positive values correspond to a higher estimated score for the perampanel condition than placebo, and negative values correspond to a lower estimated score. This direction describes the scale only; it does not itself establish clinical importance or benefit.

How should an interval and p-value be read?

An interval describes a range of effect estimates compatible with the data and the assumptions of the analysis. A broad interval indicates limited precision: the data do not pin down the contrast closely. An interval spanning zero includes no difference as well as possible differences in either direction. The recalculated intervals for both primary pairwise contrasts span zero.

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is correct, and it is not a measure of clinical importance. The registry-reported primary p-value is 0.867; the pairwise recalculated p-values are 0.938 and 0.853. Because the sponsor’s analysis and the recalculations differ in scope and method, these values should not be treated as if they came from one identical test.

What assumptions underlie the planning illustrations?

The planning illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. These are planning illustrations based on the observed data, not the original design calculation. The trial’s own sample-size assumptions and justification are not reported in the registry record. Smaller target effects require more participants under the same planning framework because a smaller separation is harder to distinguish from sampling variation.

General statistical principle: estimates, intervals, and p-values depend on the model and its assumptions. For this trial, the crossover design, repeated laboratory measures, and incomplete model description make it especially important to distinguish the sponsor’s reported mixed-model result from approximate unadjusted recalculations based on summaries.

11. Confidence Intervals and Precision

The primary point estimates are accompanied by substantial uncertainty in the recalculated pairwise comparisons. For the 6mg condition versus placebo, the estimate is 0.297 and the interval runs from -7.195 to 7.789. For the 10mg condition versus placebo, the estimate is -0.73 and the interval runs from -8.44 to 6.98. Both intervals include zero and extend in both directions, so the posted summaries do not determine a precise direction or magnitude for either pairwise difference.

A confidence interval is a range generated by a statistical procedure that, under its assumptions, reflects uncertainty in an estimated effect. Wider intervals indicate less precision. An interval spanning zero does not prove that the conditions are identical; it indicates that the data and method are compatible with no difference as well as with differences in either direction. The registry does not state the confidence level for the sponsor’s overall result, and it does not provide a confidence interval for that analysis.

The point estimates are small relative to the range of values covered by their recalculated intervals. This means that readers should not interpret the point estimates alone as a precise estimate of a perampanel-associated change. The posted arm counts for the primary measure are 14 for placebo, 17 for the 6mg condition, and 15 for the 10mg condition. Those are condition-specific counts in a crossover trial, not necessarily counts of distinct participants assigned to separate parallel groups.

The recalculated intervals rely on approximate pooled variability inferred from standard errors. They are not a substitute for intervals from the sponsor’s full mixed model, which is not available in sufficient detail in the registry record. The uncertainty should therefore be understood alongside both the limited posted sample counts and the limitations of reconstructing pairwise results from summary statistics.

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 events: the outcomes are continuous scores, and the planning illustration expresses the required count for each of two equally allocated arms. The values correspond to planning for the observed effect and for smaller fractions of that observed effect.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size justification and design assumptions are not reported in the registry record, so these figures should not be read as the trial’s planned enrollment target or as evidence of the assumptions used by its investigators.

The 80% power column describes the number of participants per arm in a hypothetical study designed to have an 80% chance of detecting the selected effect under the calculation assumptions, if that effect and those assumptions were correct. The 90% power column uses a higher target chance of detecting that effect and therefore calls for a different planning count. These are prospective planning concepts, not measures of how likely the completed trial was to find a result.

Smaller effects need more participants because they are more difficult to distinguish from random variation. The figures are illustrations based on effects observed in this trial, and those observed effects may themselves be imprecise. This is not observed power: it is a planning exercise, not a retrospective score of the trial’s success or failure.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.297; pooled standard deviation σ = 10.659.
2. n = 2 × (1.96 + 0.842)² × 10.659² / 0.297² = 20,220.3, rounded up to 20,221 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.297000000000001                      # observed difference in means
sigma <- 10.6593715380508                     # 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(2120365)
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 = 20,221 (80% power), 27,070 (90% power)
 75% of observed effect: n per arm = 35,948 (80% power), 48,124 (90% power)
 50% of observed effect: n per arm = 80,882 (80% power), 108,278 (90% power)
power.t.test: 20221.3 
Simulated power at n = 20,221 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as a mixed models analysis across placebo, perampanel 6mg, and perampanel 10mg. The registry lists a mean difference of 0.729 and p = 0.867. It does not report a confidence interval for this result or enough model detail to reproduce the analysis from the registry record.

The recalculated comparisons answer a narrower question: each perampanel dose compared separately with placebo using simple unadjusted contrasts derived from posted summary statistics. They produce estimates of 0.297 for 6mg versus placebo and -0.73 for 10mg versus placebo, with intervals and p-values that reflect that reconstruction. These pairwise calculations are not a reanalysis of the sponsor’s mixed model, and the overall reported value should not be directly equated with either pairwise estimate.

The sponsor’s result takes precedence as the trial’s own posted inferential analysis. The recalculations are useful as a transparent, approximate way to inspect pairwise differences, but they cannot account for model structure or within-person dependence that is absent from the summary statistics. Both the registry-reported analysis and the recalculated comparisons show limited evidence of a clear difference in the primary laboratory score; their methods and scope remain distinct.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators assess multiple outcomes, contrasts, time points, or subgroups. As the number of statistical tests increases, the chance of at least one result appearing unusual by chance also increases. Common approaches include adjusting significance thresholds, defining a testing hierarchy, or clearly labeling secondary analyses as exploratory. Which approach was planned for this trial is not reported in the registry record.

The registry identifies a primary endpoint and lists secondary outcomes for alcohol urge, side effects, and mood. It also reports mixed-model analyses. However, a detailed multiplicity plan, including whether or how tests were adjusted or ordered, is not reported in the registry record. The pairwise recalculations are unadjusted; they should not be interpreted as multiplicity-controlled confirmatory tests. This matters particularly for secondary outcomes, where several measures and comparisons can generate a broader set of opportunities for chance findings.

Missing-data methods are also not reported in the registry record. The listed condition-specific counts do not, by themselves, explain why the numbers vary across conditions, whether any measurements were missing, or how incomplete participant records were handled. The registry does not state whether analyses used all available observations, a defined analysis population, imputation, or another missing-data approach.

The analysis populations are not reported in enough detail to determine whether the sponsor’s analysis was based on all enrolled participants, participants who completed each laboratory condition, or another group. The reported enrollment is 22, but the primary outcome lists different condition-specific counts. In a crossover trial, those counts require context about participant completion and model inclusion; the registry record does not provide that explanation.

Interim analyses, stopping rules, and the original statistical analysis plan are not reported in the registry record. Their absence from the posted record does not establish that such procedures were or were not used. It means readers cannot assess those aspects of trial conduct from the available registry information.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry lists 22 participants at risk in each of the three safety groups. It reports zero serious adverse events in the placebo, perampanel 6mg, and perampanel 10 mg groups, and zero deaths in each group. The serious adverse event terms list is empty.

For other adverse events, the registry reports 4 affected participants in the placebo group, 1 in the perampanel 6mg group, and 4 in the perampanel 10 mg group. These are counts of participants affected, as reported, not necessarily counts of every individual event. The registry does not provide further detail about event type, severity, timing, or whether events led to treatment changes.

These figures describe the recorded safety information for this study and its listed groups. A zero count of serious events in this small study does not establish that a treatment has no serious risks. The trial’s safety counts also do not determine whether perampanel is safe or appropriate for any individual. Broader safety conclusions would require evidence beyond these registry counts and this laboratory study.

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

The primary findings describe scores on a laboratory measure of alcohol-related stimulant effects among non-treatment-seeking heavy drinkers. The posted means were 13.76 for placebo, 14.05 for perampanel 6mg, and 13.03 for perampanel 10mg. The sponsor’s mixed-model analysis reports a mean difference of 0.729 with p = 0.867. The recalculated pairwise estimates have intervals that include zero and are broad.

These results do not establish a clear difference between either perampanel condition and placebo on the primary endpoint. They also do not establish that the conditions are equivalent. The estimates are uncertain, and the registry record does not provide a prespecified equivalence margin or an analysis designed to demonstrate equivalence. A non-significant result is not proof that any possible effect is exactly zero.

The endpoint is a measure of self-reported stimulant effects during an alcohol infusion in a laboratory session. It is not an outcome measuring sustained changes in drinking, abstinence, treatment engagement, or dependence-related harms. The registry’s hypothesis about alcohol’s rewarding and reinforcing properties provides the study’s rationale, but the reported primary score is not itself a direct measure of all those properties.

The findings should be interpreted within the study’s design and information limits. It used a crossover laboratory design, enrolled 22 participants, and reports condition-specific outcome counts that vary. Details of the statistical model, missing-data handling, analysis populations, and multiplicity procedures are not reported in the registry record. Those limitations make it difficult to assess how fully the posted analyses address the repeated observations and the full set of outcomes.

Accordingly, the registry results are best understood as an account of the measured laboratory response and its uncertainty, not as a general conclusion about treatment efficacy or clinical use. They cannot show whether perampanel changes alcohol dependence or drinking behavior outside the setting studied.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a crossover design with repeated laboratory assessments. A crossover can allow comparisons within the same participant, which may reduce some between-person variability. It also creates analytical requirements: observations from one participant are related, and the model must represent that dependence appropriately. The registry names a mixed models analysis, but the details needed to assess its specification are not reported.

The trial also illustrates why a point estimate and a p-value are not enough to characterize evidence. The primary estimates are near one another, but the recalculated intervals span zero and cover a broad range. The central issue is not only whether a test crosses a conventional threshold; it is how much uncertainty remains about the size and direction of the contrast.

Another statistical lesson is the importance of matching an analysis to its question. The sponsor’s reported analysis covers all three conditions in a mixed model. Pairwise recalculations compare each dose with placebo using approximate unadjusted methods. These results can complement one another but cannot be treated as equivalent analyses. Clear reporting of the model, estimand, analysis population, and handling of repeated observations would make the distinction easier to assess.

The secondary outcomes and multiple comparisons also make multiplicity relevant. Without a stated testing strategy, secondary findings should be interpreted cautiously and in context rather than as separate confirmations. Finally, sample-size illustrations based on observed effects can show how planning needs change with a target effect, but they are not evidence of the study’s original design rationale or of observed power.

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 limitations specific to this trial affect interpretation. The study enrolled 22 participants and assessed a laboratory response in non-treatment-seeking heavy drinkers. This setting and population do not directly represent treatment outcomes or longer-term alcohol use. The primary endpoint is an averaged stimulant-effect score during a defined laboratory interval, so it captures a particular response rather than the full range of consequences associated with alcohol dependence.

The study used a crossover design with three laboratory days per participant, but the posted outcome counts vary by condition. The registry record does not explain the count differences or provide enough information to determine how incomplete observations were handled. It also does not report the analysis population, missing-data methods, or the full mixed-model specification. These gaps matter because repeated observations within participants are not independent.

The arm descriptions include incomplete text, and the registry does not report full details of the treatment schedule, washout arrangements, or period and sequence terms used in the analysis. The posted information confirms randomized order but does not permit a complete reconstruction of the crossover procedures or statistical model.

The recalculated contrasts are approximate, unadjusted comparisons based on posted summaries. Their pooled variability is inferred from standard errors, and they cannot reproduce the sponsor’s mixed model. The registry does not report confidence intervals for the sponsor’s primary analysis or a multiplicity plan for the several outcomes and comparisons. Finally, the original sample-size justification, interim analyses, and prespecified statistical analysis plan are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Rapid Determination Of The Clinical Utility Of Perampanel For The Treatment Of Alcohol Dependence — NCT02120365.
• Registry record last updated 2023-08-18; status last verified 2023-08.
• Results first posted 2023-08-18.
• 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

This completed randomized, triple-masked crossover study evaluated perampanel 6mg and 10mg versus placebo in non-treatment-seeking heavy drinkers during laboratory alcohol sessions. The registry lists 22 participants enrolled and identifies the BAES stimulant subscale as the primary outcome, averaged over the 12 to 110 minute interval and reported at the 98 minutes timeframe.

The posted primary condition means were 13.76 for placebo, 14.05 for perampanel 6mg, and 13.03 for perampanel 10mg. The sponsor’s mixed-model result was 0.729 with p = 0.867. Approximate unadjusted pairwise recalculations yielded broad intervals spanning zero for both dose comparisons with placebo. The registry also lists secondary measures of alcohol urge, side effects, and mood, and reports zero serious adverse events and zero deaths in each safety group.

The results describe a laboratory outcome and do not establish a broader clinical effect. Key details about the analysis model, missing data, analysis populations, multiplicity, and original sample-size justification are not reported in the registry record.