Study to Assess the Efficacy, Safety, and Tolerability of AVP-786 for the Treatment of Neurobehavioral Disinhibition Including Aggression, Agitation, and Irritability in Participants With Traumatic Brain Injury: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy, Safety, and Tolerability of AVP-786 for the Treatment of Neurobehavioral Disinhibition Including Aggression, Agitation, and Irritability in Participants With Traumatic Brain Injury (NCT03095066), a randomized phase 2 study. The primary outcome is Stage 1: Change From Baseline in the Composite of the Clinical Impression Severity Scores on the Neuropsychiatric Inventory Clinician Rating Scale (NPI-C) Subscale of Aggression, Agitation, and Irritability/Lability (NPI-C-3).

2. Clinical Question

The primary endpoint is a continuous score, analyzed as a least-squares mean in the modified intent-to-treat population. The posted Stage 1 estimates were -20.4 for AVP-786 and -18.7 for placebo. The sponsor’s reported difference in least-squares means was -1.7, with a 95% confidence interval from -5.8 to 2.4 and p = 0.405. The interval includes no difference, so the estimate is not precise enough to establish a clear difference between the groups from this result alone. These results describe the measured endpoint over the stated timeframe; they do not by themselves establish effects on every symptom or outcome of interest.

3. Trial Design

This was a Phase 2, multicenter, randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Otsuka Pharmaceutical Development & Commercialization, Inc. The registry lists an enrollment of 168 and a completed status. The study began on 2017-05-30, and primary completion was recorded as 2022-08-22. The purpose was to assess the efficacy, safety, and tolerability of AVP-786 for neurobehavioral disinhibition, including aggression, agitation, and irritability, in participants with traumatic brain injury.

The design included two stages. In Stage 1, participants received placebo or AVP-786. The primary endpoint compares change from baseline to Week 6, the end of the stated Stage 1 primary timeframe. The registry describes classification as responder or non-responder after Week 6, followed by re-randomization to Stage 2 treatment for participants initially assigned placebo. The response criteria in the record refer to the modified Clinical Global Impression of Severity and change in the NPI-C-3 score. The full Stage 2 treatment description and complete dosing schedule are not reported in the registry record.

The posted primary analysis concerns Stage 1, not a combined estimate across both stages. It used a modified intent-to-treat population defined by randomization, receipt of at least one dose, and at least one post-baseline NPI-C-3 assessment during Stage 1. The record reports 64 analyzed participants for placebo and 61 for AVP-786 for this endpoint. These analysis counts describe participants with data available for the primary analysis; they should not be confused with the registry’s overall enrollment.

Eight secondary outcome measures are listed, including NPI-C subscales for aggression, agitation, irritability/lability, and disinhibition, as well as clinician and patient global impression measures. The registry record does not report the original sample-size justification, the trial’s prespecified statistical plan in detail, or whether interim analyses were conducted.

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: Study was conducted in 2 Stages. Participants randomized to receive placebo in Stage 1 were re-randomized after Week 6 to receive either placebo or AVP-786 in Stage 2. As pre-specified in protocol, participants randomized to 'AVP-786' arm were not re-randomized after Week 6 and continued receiving AVP-786 in the same arm throughout 12 weeks of study. Study is presented in 3 stages: Overall Study, Stage 1 \& Stage 2.

Only the first 6 of 8 groups are shown.

Overall Study (Baseline to Week 12)

Reasons for not completing this period:

Stage 1 (Baseline to Week 6)

Reasons for not completing this period:

Stage 2 (Week 7 to Week 12)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (mITT) population. Stage 1: Participants randomized in Stage 1 who took at least 1 dose of study medication \& had at least 1 post-baseline NPI-C-3 composite score efficacy assessment in Stage 1. Overall number analyzed=participants with data available for analysis.

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: Safety population included all participants who received at least one dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Stage 1: Change From Baseline in the Composite of the Clinical Impression Severity Scores on the Neuropsychiatric Inventory Clinician Rating Scale (NPI-C) Subscale of Aggression, Agitation, and Irritability/Lability (NPI-C-3), measured over Baseline to Week 6.

The primary endpoint was change from baseline to Week 6 in the composite of the NPI-C clinician impression severity scores for aggression, agitation, and irritability/lability. The NPI-C is a retrospective interview involving an informant or caregiver and the participant, with the clinician integrating information into severity ratings. The composite, called NPI-C-3, ranges from 0 to 99; higher scores indicate increased severity.

Combining these three symptom domains gives a single continuous outcome focused on the neurobehavioral features named in the trial’s objective. A change score expresses how the measured composite shifted from each participant’s baseline, while the comparison of group means addresses whether average change differed between treatment groups. In this trial, the least-squares means were analyzed with a mixed-effects model for repeated measures. Least-squares means are model-based group estimates, rather than simple arithmetic averages alone.

The endpoint is useful for quantifying change on the specified composite, but it does not represent every aspect of traumatic brain injury or every secondary symptom. The outcome definition also matters when interpreting direction: a more negative change corresponds to a larger decrease in the measured score, and higher scores indicate greater severity. The posted estimates therefore describe change on this scale over the stated Stage 1 period, not a general measure of recovery.

7. Results Posted in the Registry

• Stage 1: AVP-786: mean -20.40 versus -18.70 on control; difference -1.70 (95% CI -6.51 to 3.11), standardized effect d = -0.12; z-test p = 0.488.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: each participant’s NPI-C-3 composite is measured as a score, and the analysis concerns change from baseline to Week 6. The registry reports least-squares means and standard errors for the group estimates, and identifies a mixed-effects model for repeated measures (MMRM) as the analysis method. In general, a continuous-outcome analysis estimates average values or changes and compares those estimates between groups. The effect estimate is expressed in the original score units, which makes its direction interpretable alongside the scale definition.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based estimate of a group mean. It is obtained from the fitted model rather than being only the raw arithmetic average. This can be useful when the analysis uses observations collected at repeated visits or accounts for the structure of the data. The registry identifies the primary parameter as a least-squares mean, but does not report the full model specification, the included covariates, or the exact covariance structure. Those details should not be inferred from the name MMRM alone.

Why use a repeated-measures model?

In general, repeated-measures models are used when measurements are collected from the same participants across time. Measurements from one participant are related, so treating every visit as independent would fail to reflect that structure. An MMRM can use repeated outcome observations to estimate group patterns over time and can compare model-based changes at a specified visit. Here, the primary timeframe is baseline to Week 6. The registry does not state the visit schedule used in the fitted model or all assumptions used for estimation.

In general, such models can accommodate incomplete outcome histories under assumptions about the missingness process, but the model name alone does not establish that those assumptions hold. The registry’s primary analysis population requires at least one post-baseline efficacy assessment. It does not report detailed missing-data diagnostics, sensitivity analyses, or a full account of how participants with incomplete visit data contributed. Accordingly, the posted MMRM result should be interpreted as the model-based estimate for the stated analysis population, without assuming that all missing-data concerns have been resolved.

How should the difference and p-value be read?

The sponsor reports a difference in least-squares means of -1.7 for AVP-786 compared with placebo. In general, a difference is a contrast between group estimates, and zero represents no difference on the scale of that contrast. The reported p-value is 0.405. In general, a p-value measures how unusual the observed result, or a more extreme one, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure clinical importance.

The sponsor’s 95% confidence interval for the difference is -5.8 to 2.4. In general, a confidence interval communicates the precision of an estimate by giving a range of values compatible with the data and the analysis procedure. An interval that crosses zero does not establish a between-group difference at the corresponding two-sided threshold. It also does not establish that the groups are equivalent; equivalence would require an appropriate design, margin, and analysis, which are not reported in the registry record.

Why can a simple recalculation differ?

A recalculation from posted group summary statistics uses a simpler, unadjusted comparison. The calculation reported for this endpoint uses the group estimates and standard errors and gives a mean difference of -1.7, a 95% confidence interval from -6.509 to 3.109, and an unadjusted p-value of 0.488. These are not the sponsor’s MMRM results. A model-based repeated-measures analysis may use information and assumptions not represented by a simple calculation from summary statistics. The record does not give enough model detail to attribute the difference between the intervals to any one feature. For interpretation, the sponsor’s reported MMRM analysis is the relevant trial analysis.

Over-dispersion is a general concern when variability exceeds what a statistical model assumes. In general, underestimated variability can make intervals too narrow and tests appear more decisive than the data warrant. The registry does not report an over-dispersion assessment for this endpoint, and the simple recalculation uses an approximate pooled standard deviation. It should therefore be treated as a check based on posted summaries, not as a replacement for the sponsor’s model.

The trial is randomized and masked, features that are intended in general to reduce systematic differences in treatment assignment and outcome assessment. They do not eliminate uncertainty from sampling variability, missing data, analysis choices, or multiple outcome testing. The registry record does not report the detailed randomization procedure, the full masking arrangements beyond the quadruple-masked designation, or the prespecified analysis plan. These limits make it important to distinguish the posted model result from broader conclusions not established by the record.

10. Confidence Intervals and Precision

The sponsor’s estimated difference in Stage 1 least-squares mean change was -1.7 points on the NPI-C-3 scale. Its 95% confidence interval runs from -5.8 to 2.4. The interval crosses zero, so the posted result is compatible with no between-group difference as well as with differences in either direction. It gives a sense of the uncertainty around the estimate; it should not be read as a range containing a known fixed treatment effect with certainty.

The width of this interval matters as much as the point estimate. The observed estimate is relatively close to zero compared with the range of values left plausible by the interval. The result therefore does not precisely determine the size or direction of a group difference. The reported p-value, 0.405, is consistent with that uncertainty, but it does not quantify the probability that there is no effect or that the result is due to chance.

The simple summary-statistic recalculation has a 95% confidence interval from -6.509 to 3.109, with an unadjusted p-value of 0.488. Its point estimate is also -1.7. The different interval reflects that it is a recalculation rather than the sponsor’s MMRM analysis; the two should not be combined or treated as interchangeable. The sponsor’s reported MMRM result is the primary trial analysis.

Precision is influenced by the amount and variability of usable outcome information, as well as by the analysis model. The primary analysis included 64 placebo participants and 61 AVP-786 participants. The registry record does not report a confidence interval for each group mean in the outcome listing, a prespecified clinically important difference, or the trial’s original sample-size rationale. Without a stated threshold for meaningful change, the interval can be described statistically but cannot be classified against a registry-reported clinical relevance boundary.

11. Planning a Similar Trial: Sample Size

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

The planning values translate the observed effect into illustrative future-study sizes; they do not describe the number enrolled or analyzed in this trial. For this continuous outcome, the figures are participants per arm, not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the assumptions used in the trial’s original design or its original sample-size justification.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding illustrative number per arm for a 90% chance. These are design-planning probabilities under a statistical model, not guarantees about a future result. The figures are based on the observed effect, which is uncertain, so they should not be treated as definitive requirements for a new study.

The rows set the target effect to 100%, 75%, and 50% of the observed effect. The displayed planning values increase as the target becomes a smaller fraction of the observed effect: detecting a smaller difference generally requires more participants. The same direction is apparent in a planning curve when it maps sample size against the effect being targeted. That relationship is general; the precise estimates depend on the stated planning assumptions.

This is not observed power. Observed power is not a useful substitute for reading the actual estimate and its confidence interval, and the planning illustration does not show the probability that the trial result is true. These values are scenario-based planning illustrations, distinct from the registry’s enrollment and the primary endpoint analysis counts.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -1.700; pooled standard deviation σ = 13.722.
2. n = 2 × (1.96 + 0.842)² × 13.722² / -1.700² = 1,022.8, rounded up to 1,023 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -1.7                      # observed difference in means
sigma <- 13.7223623792805                     # 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(3095066)
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 = 1,023 (80% power), 1,370 (90% power)
 75% of observed effect: n per arm = 1,819 (80% power), 2,435 (90% power)
 50% of observed effect: n per arm = 4,092 (80% power), 5,478 (90% power)
power.t.test: 1023.8 
Simulated power at n = 1,023 per arm: 0.802 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor’s primary Stage 1 analysis used an MMRM and reported a difference in least-squares means of -1.7, a 95% confidence interval from -5.8 to 2.4, and p = 0.405. This is the trial’s reported model-based analysis and should be the main inferential result when describing the registered outcome.

A simple recalculation from posted summary statistics gives the same point estimate, -1.7, but a 95% confidence interval from -6.509 to 3.109 and an unadjusted p-value of 0.488. The recalculation is not an MMRM and does not reproduce the sponsor’s full model. The different interval and p-value therefore should be understood as a difference between an unadjusted summary-based calculation and the sponsor’s reported repeated-measures analysis, not as competing sponsor results.

Both analyses leave the estimate uncertain and have intervals that include zero. The registry does not identify a discrepancy between the recalculation and the reported result. Even so, the model-based sponsor analysis takes precedence for interpretation of the trial’s prespecified primary analysis; the simple recalculation serves only as a transparent check using the posted summaries. Neither result alone establishes equivalence or determines clinical importance.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists eight secondary outcome measures in addition to the primary endpoint and reports 18 analyses. Multiple outcomes and analyses create a multiplicity issue: when many hypotheses are tested, the chance of at least one apparently unusual result can increase. In general, investigators may address this through prespecified testing hierarchies, adjusted thresholds, or other strategies. The registry record does not report whether multiplicity adjustment was used, how the listed analyses were ordered, or which analyses were prespecified. The primary p-value should therefore be interpreted as reported, without assuming that it was adjusted for the wider set of outcomes.

The primary analysis population is described as modified intent-to-treat. It includes Stage 1 participants who were randomized, took at least one dose, and had at least one post-baseline NPI-C-3 efficacy assessment in Stage 1. The number analyzed is defined as participants with data available for analysis. This is not a full account of all randomized participants’ outcome availability, and the registry does not provide a participant-flow explanation for exclusions from this endpoint analysis.

The endpoint was analyzed using MMRM. In general, repeated-measures models can make use of available measurements, but valid interpretation depends on model specification and assumptions about missingness. The registry does not report the detailed missing-data strategy, the pattern or reasons for missing observations, sensitivity analyses, or whether the assumptions were assessed. It is therefore not possible to determine from this record alone how robust the estimate is to alternative assumptions about missing data.

The record also does not report whether interim analyses occurred, the full prespecified statistical analysis plan, or a complete account of model covariates and covariance structure. These omissions do not change the reported estimate, but they limit independent assessment of the analysis choices and of how the primary result fits within the overall testing plan. Interpretations should remain focused on the posted Stage 1 comparison and its stated analysis population.

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: cholecystitis acute (0.9%), enterobacter sepsis (0.9%), seizure (0.9%).

The registry reports serious adverse event figures for All Placebo and All AVP-786. In the placebo group, 83 were at risk and 0 had a serious adverse event; in the AVP-786 group, 115 were at risk and 3 had a serious adverse event. Deaths were 0 in both groups. For other adverse events, 4 of 83 were affected in the placebo group and 7 of 115 in the AVP-786 group. These are the posted counts and denominators; they should be read as safety summaries, not as proof that an event was caused by treatment or that no unlisted event occurred.

The serious-event terms listed at 0.9% each are Cholecystitis acute, Enterobacter sepsis, and Seizure. The record excerpt does not assign each term to a treatment group, so group attribution should not be inferred. Serious adverse events are distinct from the broader category of other adverse events, and the event counts do not by themselves describe severity, timing, duration, or relatedness.

The groups’ safety summaries are descriptive. Differences in counts cannot be interpreted causally without fuller context on exposure, follow-up, event definitions, and statistical methods, which are not reported in the registry record. These figures should be understood alongside the trial’s overall safety reporting rather than as a complete safety profile.

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

The primary result describes change in a defined symptom composite over Stage 1, from baseline to Week 6. Both groups had negative estimated changes, and the AVP-786 group’s least-squares mean estimate was -20.4 compared with -18.7 for placebo. The sponsor’s estimated between-group difference was -1.7. Because higher NPI-C-3 scores indicate increased severity, the negative direction corresponds to a greater estimated decrease in the AVP-786 group, but the confidence interval shows that this contrast is uncertain.

The sponsor’s 95% confidence interval, -5.8 to 2.4, includes zero. The reported p-value of 0.405 does not provide strong statistical evidence of a between-group difference under the analysis used. This does not prove that the groups are identical, that AVP-786 has no effect, or that a clinically important difference is impossible. It means the posted estimate is not precise enough to settle those possibilities. The registry does not report a threshold for clinically important change on this endpoint.

The result is specific to the NPI-C-3 composite, the Stage 1 period, and the modified intent-to-treat population. It should not be generalized automatically to every symptom domain, to the later stage, or to all participants with traumatic brain injury. Secondary outcomes include separate symptom subscales and global impression measures, but the record does not report the multiplicity strategy needed to interpret a broad set of tests as a unified claim.

The reported safety counts are also descriptive and cannot establish causation or a complete account of risks. More broadly, the registry record does not provide enough information to assess all missing-data assumptions, the full statistical analysis plan, or the original design assumptions. The most defensible reading is therefore limited: the posted Stage 1 analysis estimates a small difference on the specified score, with uncertainty spanning values on either side of no difference. It neither establishes a benefit nor demonstrates equivalence.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated group difference cannot be interpreted by its direction alone. The Stage 1 estimate favors a larger decrease in the AVP-786 group on the NPI-C-3 scale, but its confidence interval includes zero and extends to values in the opposite direction. Reporting the point estimate together with its interval gives a more informative account than treating the sign of the estimate or p-value as a complete conclusion.

It also highlights the distinction between a sponsor’s model-based primary analysis and a simple recalculation from summary statistics. Both produce a point estimate of -1.7, while their intervals and p-values differ. The sponsor’s MMRM uses a repeated-measures framework, whereas the recalculation is unadjusted and based on posted summaries. Recognizing that distinction helps readers avoid treating a transparent approximation as if it were the trial’s full analysis.

The design’s staged structure and responder re-randomization make it especially important to identify which part of the study a result addresses. The primary endpoint is explicitly a Stage 1 comparison from baseline to Week 6. It is not a result for all stages combined. A clear statement of timeframe, population, outcome definition, and model prevents the primary estimate from being generalized beyond what it measures.

Finally, the record lists multiple secondary outcomes and analyses, but does not report multiplicity handling or detailed missing-data methods. These are not minor technicalities: they affect how confidently a reader can interpret a single p-value in the context of the broader evidence. The trial is a useful example of statistical interpretation that keeps the estimate, its precision, its analysis population, and the limits of the registry record in view.

18. Limitations

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

The primary result is limited to Stage 1 change from baseline to Week 6 on the NPI-C-3 composite. The registry does not provide a reported clinically important difference for this scale, so the clinical importance of the estimated contrast cannot be judged against a stated threshold. The composite also combines aggression, agitation, and irritability/lability; a single estimate does not show whether the individual domains changed in the same way.

The primary analysis population was modified intent-to-treat and required at least one dose and at least one post-baseline assessment. The record gives the analyzed counts but does not give a complete participant flow for this endpoint or detailed information about missing observations. It reports MMRM but not the full model specification, missing-data assumptions, sensitivity analyses, or diagnostics. These gaps limit assessment of how robust the estimate is to analytic choices.

The study had a staged design, including responder classification and re-randomization after Week 6 for participants initially assigned placebo. The primary result does not summarize Stage 2, and the available record does not give the full Stage 2 dosing description. Results from Stage 1 should not be interpreted as an estimate of the entire staged treatment strategy.

The registry lists eight secondary measures and 18 analyses but does not report the multiplicity strategy or a complete statistical analysis plan. It also does not report the original sample-size justification, interim analyses, or the trial’s own planning assumptions. The sample-size illustration based on the observed effect is not a substitute for the original design rationale. Finally, safety counts are descriptive, and the listed serious adverse event terms are not assigned to treatment groups in the available record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy, Safety, and Tolerability of AVP-786 for the Treatment of Neurobehavioral Disinhibition Including Aggression, Agitation, and Irritability in Participants With Traumatic Brain Injury — NCT03095066.
• Registry record last updated 2025-10-29; status last verified 2025-10.
• Results first posted 2025-10-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03095066 was a completed Phase 2, multicenter, randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Otsuka Pharmaceutical Development & Commercialization, Inc. It evaluated AVP-786 for neurobehavioral disinhibition in participants with traumatic brain injury. The primary endpoint was change from baseline to Week 6 in the NPI-C-3 composite of aggression, agitation, and irritability/lability.

The Stage 1 analysis used a modified intent-to-treat population and an MMRM. The sponsor reported a difference in least-squares means of -1.7, with a 95% confidence interval from -5.8 to 2.4 and p = 0.405. The interval includes zero, leaving uncertainty about the direction and size of the group difference. The registry also lists secondary symptom and global impression outcomes, but does not report multiplicity handling, detailed missing-data methods, or the trial’s original sample-size rationale.