Study to Test the Efficacy and Safety of Vafidemstat in Adult Borderline Personality Disorder Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Test the Efficacy and Safety of Vafidemstat in Adult Borderline Personality Disorder Population (NCT04932291), a randomized phase 2 study. The primary outcome is Efficacy: Difference in the CGI-S A/A From Baseline to Average of Weeks 8 to 12.

2. Clinical Question

3. Trial Design

PORTICO is registered as a randomized, double-blind, parallel-group Phase IIb trial of vafidemstat in an adult BPD population. The registry lists 211 participants enrolled, with 106 assigned to vafidemstat 1.2 mg and 105 to placebo for the primary outcome. The study status is completed. The registry lists a start date of 2021-03-26 and a primary completion date of 2023-10-30.

Both arms received capsules, with placebo serving as the control. Randomization and double masking are stated, but the method used to generate the allocation sequence, concealment procedures, and the identities of people masked are not reported in the registry record. The official title describes the trial as adaptive, but the adaptation rules, whether any adaptation was implemented, and any consequences for enrollment or analysis are not reported in the registry record.

The primary outcome concerns change in CGI-S A/A from baseline to the average of Weeks 8 to 12. The registry also lists secondary efficacy outcomes spanning BPD symptoms, depression, anger, anxiety, clinical severity over time, and a BPD checklist score. It records 18 outcome measures and 17 analyses, while 16 secondary outcomes are identified as posted. The registry record does not explain the relationship between those counts or provide full numerical results for every listed secondary outcome.

This design supports a randomized comparison of the two assigned arms. It does not, by itself, establish that all participants completed treatment or contributed data at every assessment. Detailed follow-up, adherence, and analysis-population rules are not reported in 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Full analysis set

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: Full analysis set population

6. Primary Endpoint

The registry lists the primary outcome as Efficacy: Difference in the CGI-S A/A From Baseline to Average of Weeks 8 to 12, measured over From Baseline-Week 0 to average of Weeks 8 to 12.

The primary endpoint is change on the Clinical Global Impression-Severity focused on Agitation/Aggression (CGI-S A/A), comparing baseline with the average of Weeks 8 to 12. It is a clinician's global rating of the severity of a participant's BPD-related agitation and aggression symptoms at the time of evaluation. The measure has one item and ranges from 0 to 7; higher scores indicate greater symptom severity.

A clinician-rated global measure is used to summarize an overall judgment of the target symptom domain rather than one narrow behavior or a participant's self-rating alone. Assessing change from baseline focuses the comparison on how scores shift over the treatment period. Using an average across Weeks 8 to 12 is intended to represent scores across that interval rather than a single assessment at one week. These are general features of such outcome measures; the rationale for selecting this specific endpoint and time window is not reported in the registry record.

The registry reports least-squares mean changes of -1.47 for vafidemstat and -1.31 for placebo. The comparison is a mean difference, with the reported direction corresponding to vafidemstat minus placebo. The estimate and its confidence interval should be considered together: the estimate alone does not establish how precisely the arm contrast is known.

7. Results Posted in the Registry

• Vafidemstat 1.2mg: mean -1.47 versus -1.31 on control; difference -0.16 (95% CI -0.47 to 0.15), standardized effect d = -0.14; z-test p = 0.308.

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.

Efficacy: Difference in the BEST-Total Score From Baseline to Average of Weeks 8 to 12

• 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:
  • Vafidemstat 1.2mg: mean -11.30 versus -8.64 on control; difference -2.66 (95% CI -5.57 to 0.25), standardized effect d = -0.25; z-test p = 0.073.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vafidemstat 1.2mg and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy: Difference in the BDI-II Total Score From Baseline to Average of Weeks 8 to 12

• 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:
  • Vafidemstat 1.2mg: mean -8.79 versus -6.18 on control; difference -2.61 (95% CI -6.38 to 1.16), standardized effect d = -0.19; z-test p = 0.175.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vafidemstat 1.2mg and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy: Difference in the STAXI-2-State Anger Subscale Score From Baseline to Average of Weeks 8 to 12

• 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:
  • Vafidemstat 1.2mg: mean -4.87 versus -4.30 on control; difference -0.57 (95% CI -3.01 to 1.87), standardized effect d = -0.06; z-test p = 0.647.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vafidemstat 1.2mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures covering BPD symptoms, depressive symptoms, anger, anxiety, clinical global severity over time, and a BPD checklist score. The detailed posted results are incomplete relative to the full list of registered measures, so the pattern cannot be characterized comprehensively from the available numerical results. Among the secondary results with detailed comparisons, estimates generally favor a greater decrease in the vafidemstat arm, but their precision and sponsor-reported evidence vary.

The detailed BEST result is the clearest contrast in the posted secondary analyses: the sponsor reports a mean difference of -2.67, with a 95% confidence interval from -5.02 to -0.32 and p=0.026. The simple recalculation is less conclusive, with an interval from -5.57 to 0.250 and unadjusted p=0.073. For the BDI-II result, the sponsor's interval spans zero and p=0.094. The STAXI-2-State result has a sponsor-reported interval spanning zero; the registry lists its p-value as -0.568, which is outside the possible range for a probability and should be treated as a registry-record anomaly rather than a valid p-value.

These secondary measures address related but distinct symptom domains, while the primary outcome specifically concerns clinician-rated agitation/aggression severity. They may help describe the range of outcomes assessed, but they do not replace the prespecified primary comparison. A secondary finding does not establish the primary result, and a secondary outcome with a more favorable result should not be read as a confirmatory conclusion without the trial's testing plan.

Many outcomes create a multiplicity concern: the more statistical tests considered, the greater the chance that at least one appears notable by chance if no adjustment is made. The listed secondary recalculations are unadjusted, and the multiplicity procedure, if any, is not reported in the registry record. This makes isolated secondary p-values less persuasive than a result interpreted under a prespecified plan that accounts for all relevant tests. The registry also does not provide detailed numerical results for all listed secondary outcomes, limiting assessment of consistency across measures.

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

• Efficacy: Difference in the BEST-Total Score From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the BDI-II Total Score From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the STAXI-2-State Anger Subscale Score From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the STAXI-2-Trait Anger Subscale Score From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the STAXI-2-Anger Expression Index Subscale Score From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the STAI-State Anxiety From Baseline to Average of Weeks 8 to 12
• Efficacy: Difference in the CGI-S A/A Over Time (From Baseline to Week 12)
• Efficacy - Difference in the BPDCL-Total Score Over Time (From Baseline to Week 12)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: it is a numerical score, and the registry reports least-squares mean changes and a mean difference between arms. In general, a mean summarizes the center of a set of numerical observations. A least-squares mean is a model-based mean, often adjusted for features included in the model. The registry names least-squares means for the arm results and a mixed-model analysis for the sponsor's comparison, but the covariates and full model specification are not reported in the registry record.

What does a between-arm mean difference represent?

The comparison is expressed as vafidemstat minus placebo. The reported estimate of -0.16 means that the estimated change in the vafidemstat arm was lower than the estimated change in the placebo arm by that amount on the CGI-S A/A score. Since lower scale scores indicate less symptom severity, the direction of this point estimate is consistent with a larger average decrease in the active-treatment arm. The sign describes direction, not certainty, clinical importance, or causation on its own.

The posted arm estimates are -1.47 for vafidemstat and -1.31 for placebo. Both represent decreases from baseline. A comparison between arms is more informative about the randomized treatment contrast than looking at change in one arm alone, because change can occur in both groups over time for reasons that include the course of symptoms, trial participation, and measurement variation. These are general considerations; the registry does not provide a decomposition of why participants' scores changed.

Why report a confidence interval?

A confidence interval describes uncertainty around an estimate under the assumptions of the analysis. In repeated use of the same method, intervals constructed this way would cover the target value at the stated rate. It is not a range that guarantees where the true value lies in this particular trial, nor does it give the probability that the treatment has a particular effect. For the primary sponsor analysis, the 95% interval is -0.42 to 0.1. The recalculated interval is -0.468 to 0.148. Both span zero, so both allow for no average difference as well as differences in either direction.

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 true, and it does not measure the size or clinical importance of an effect. The sponsor reports p=0.227 for the primary comparison, while the simple unadjusted recalculation gives p=0.308. Neither value should be interpreted in isolation from the estimate, interval, model, and outcome context.

Why do the recalculation and sponsor result differ?

The recalculation is based on the posted arm summaries and is unadjusted. The record identifies each arm's dispersion as a standard error and notes that a pooled standard deviation used for recalculation is approximate. A standard error describes the uncertainty of an estimated mean, whereas a standard deviation describes variation among individual scores; they are not interchangeable. The recalculation derives an approximate comparison from the available summaries and cannot reproduce an analysis that uses participant-level repeated measurements or model adjustments.

The sponsor's primary analysis is identified as a mixed-model analysis of mean difference in final values. In general, a mixed model can account for correlations among repeated measurements from the same participant and can use data across visits under model assumptions. The registry does not report the model formula, covariance structure, covariates, missing-data assumptions, or exact observations included. The label alone is not enough to determine how those choices affected the estimate.

The record lists the primary population as the full analysis set. This label indicates the intended analysis population, but its operational definition and rules for retaining participants after randomization are not reported in the registry record. It would be inappropriate to assume a particular intention-to-treat definition or to infer how missing values were handled from the population label alone.

Why do score direction and scale matter?

The CGI-S A/A ranges from 0 to 7, with higher scores reflecting greater severity. This makes the negative arm changes and the negative between-arm estimate interpretable as decreases in the rating. The scale's range also gives context for the units, but the registry does not report a minimum clinically important difference or a responder threshold. Statistical evidence about an average contrast cannot substitute for those clinical interpretation criteria.

All these explanations describe general statistical concepts. The trial's detailed statistical analysis plan, prespecified hypothesis-testing procedure, multiplicity strategy, and missing-data methods are not reported in the registry record. As a result, interpretation should distinguish the sponsor's reported model result from the supplementary, summary-statistic recalculation.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is a mean difference of -0.16, with a 95% confidence interval from -0.42 to 0.1. The simple recalculation gives the same point estimate, -0.16, with an interval from -0.468 to 0.148. Both intervals cross zero. In practical terms, the data do not estimate the primary contrast with enough precision to exclude no average difference under either reported interval.

The interval also indicates that the estimate is compatible with differences in either direction. Its width reflects uncertainty in the estimated contrast, not the spread of individual participants' scores. The registry reports standard errors of 0.111 for each arm's least-squares mean; these describe uncertainty around the arm means, not participant-to-participant variability. A confidence interval is generally more informative than a point estimate alone because it makes the range of values reasonably compatible with the analysis visible.

The sponsor's interval comes from the reported mixed-model analysis, while the recalculated interval is an approximate, unadjusted result derived from posted summaries. The latter relies on an approximate pooled standard deviation. It should not be treated as a more definitive interval just because it has more decimal places. The sponsor's model is the trial's own analysis, and the registry record does not give the full model specification needed to independently reproduce it.

The interval addresses statistical precision for the group contrast; it does not establish clinical importance. The registry does not report a threshold for a meaningful CGI-S A/A change. It also does not provide a prediction interval for individual outcomes. Thus, the result should not be used to infer that individuals would experience a change equal to the group mean.

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 illustrations concern participants per arm, not total participants or total events. The outcome is continuous, so the relevant figures are participants per arm. The illustrations use the observed mean difference as a reference and consider planning for 100%, 75%, and 50% of that observed effect. They are not the trial's original enrollment calculation; the trial's own sample-size justification and design assumptions are not reported in the registry record.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustrations use an effect equal to the stated fraction of the observed effect. Under those assumptions, the 80% power column describes the number of participants per arm that would give an 80% chance of detecting the chosen effect if that effect and the assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance.

These are forward-looking design calculations, not evidence about the chance that this completed trial found an effect. They are not observed power. Smaller effects generally require more participants to distinguish them from random variation at the same significance level and target power. That relationship is why planning for a smaller fraction of the observed effect produces larger participant requirements.

The calculations are simplified illustrations. They do not incorporate details that might arise in the sponsor's mixed model, such as repeated-measure correlations, covariate adjustments, attrition, or a multiplicity strategy. Whether any such considerations were included in the original design cannot be established because the original assumptions are not reported in the registry record. The illustrations should therefore be read as conditional examples under their stated assumptions, rather than as a reconstruction of the trial's actual design process.

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 = -0.160; pooled standard deviation σ = 1.140.
2. n = 2 × (1.96 + 0.842)² × 1.140² / -0.160² = 797.1, rounded up to 798 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 <- -0.16                      # observed difference in means
sigma <- 1.14012936813177                     # 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(4932291)
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 = 798 (80% power), 1,068 (90% power)
 75% of observed effect: n per arm = 1,418 (80% power), 1,898 (90% power)
 50% of observed effect: n per arm = 3,189 (80% power), 4,269 (90% power)
power.t.test: 798 
Simulated power at n = 798 per arm: 0.800 (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 own primary analysis is a mixed-model analysis. It reports a mean difference of -0.16, a 95% confidence interval from -0.42 to 0.1, and p=0.227. The registry's arm summaries also permit a simple, unadjusted recalculation, which gives a mean difference of -0.16, a confidence interval from -0.468 to 0.148, and p=0.308.

The point estimates agree, while the intervals and p-values differ. That is not unexpected when an approximate calculation from summary statistics is compared with a participant-level mixed-model analysis: the calculations can use different information and assumptions. The registry does not report enough detail about the mixed model to reproduce the sponsor's result independently. The recalculated interval also relies on an approximate pooled standard deviation.

The sponsor result is the trial's reported analysis and should be the main reference for the study's primary statistical result. The recalculation is useful as a transparent, limited check based on the summaries, but it is not an alternative sponsor analysis and does not supersede the reported model. Both results have intervals spanning zero, so neither offers a precise estimate that excludes no average difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry describes a primary outcome and numerous secondary outcomes, including measures of BPD symptoms, depression, anger, anxiety, and clinical severity. Testing many outcomes raises a general multiplicity issue: when multiple hypotheses are examined, the chance of at least one apparently favorable result can increase. A prespecified hierarchy, adjustment procedure, or clearly defined exploratory interpretation can help readers understand how such results should be weighed.

The multiplicity strategy and the complete statistical analysis plan are not reported in the registry record. It is therefore not possible to determine whether the secondary analyses were adjusted, whether some outcomes were designated as confirmatory, or how the testing order was defined. The unadjusted recalculated results should not be treated as if they account for the number of outcomes considered.

The primary analysis population is named as the full analysis set, but its definition is not reported in the registry record. The number contributing to each specific endpoint and the rules for inclusion after randomization are not fully described. The primary arm summaries list 106 participants for vafidemstat and 105 for placebo, while adverse-event risk sets use different arm counts; outcome and safety populations need not be identical.

Missing-data methods are also not reported in the registry record. The record does not specify how missed visits or incomplete outcome scales were handled, what assumptions were made about unobserved scores, or whether sensitivity analyses tested those assumptions. This matters because a mixed model can use available repeated observations, but its interpretation depends on model assumptions about the data that are missing. No particular missing-data procedure should be inferred from the term mixed model alone.

The title describes an adaptive trial, but the adaptation rules and any effect on the analyses are not reported in the registry record. Details of interim analyses, stopping criteria, or changes to the design are likewise not reported. These absences limit a full audit of prespecification and statistical control; they do not by themselves establish that the trial's analyses were improperly conducted.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: kidney infection (0.9%).

The registry reports serious adverse events for 1 participant in the vafidemstat safety risk set of 106 and 0 participants in the placebo risk set of 104. It lists kidney infection at 0.9% as the leading serious adverse-event term. Deaths are recorded as 0 in each arm. These are descriptive counts in the registry, not estimates adjusted for follow-up duration or other factors.

The record also reports other adverse events for 27 participants in the vafidemstat risk set and 40 in the placebo risk set. Those events are distinct from the serious adverse-event counts and should not be combined with them. The registry does not provide enough detail to assess event duration, severity grading, attribution to study treatment, timing, or individual clinical context.

Safety counts require cautious interpretation. A recorded count does not establish that an event was caused by the assigned treatment, and zero recorded deaths does not demonstrate an absence of every possible safety risk. The study's duration and observed participants constrain what these data can reveal. These figures describe the registry record and are not medical advice.

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

The primary result describes an average between-arm difference in change on a clinician-rated measure of agitation/aggression severity. The point estimate is -0.16, and the sponsor's 95% confidence interval spans -0.42 to 0.1. The data are therefore compatible with no average difference as well as with values in either direction. The registry result does not establish a precise treatment effect on this measure.

That interpretation is narrower than saying whether vafidemstat works or does not work. A confidence interval crossing zero is not proof that the treatments are identical, just as a negative estimate is not proof that the observed difference was caused by treatment. The size of any difference that would matter clinically is also not established: a clinically important threshold is not reported in the registry record.

The endpoint is one clinician-rated, single-item score focused on agitation and aggression, measured over a particular period. It does not capture every feature of BPD, every outcome important to participants, or long-term outcomes. The registered secondary outcomes expand the range of domains considered, but the record does not report full numerical results for every listed outcome or the multiplicity procedure.

The randomized, double-blind, placebo-controlled design is relevant to evaluating the comparison, but some details needed to judge the analysis are absent from the registry record. The definitions of analysis populations, missing-data handling, detailed mixed-model specification, and adaptive procedures are not reported. Those omissions limit independent assessment of how robust the estimates are to analysis choices.

Finally, group averages do not predict an individual's response, and safety event counts do not determine whether a treatment is appropriate for a particular person. These results are a statistical account of the registered trial outcomes, not medical advice or a recommendation about care.

18. Why This Trial Matters Statistically

This trial is statistically informative because it puts a randomized placebo comparison around a defined symptom-domain outcome: clinician-rated agitation/aggression severity. The primary measure, time window, arm estimates, and sponsor-reported analysis make the central contrast interpretable. The direction and size of an estimate can be discussed alongside its uncertainty rather than in isolation.

The primary contrast is modest in relation to its uncertainty: the sponsor's confidence interval includes zero, and the simple summary-statistic recalculation reaches the same broad conclusion about precision. This distinction matters. A point estimate gives a single best estimate under a method, whereas the interval communicates that the true average contrast remains uncertain. Neither an uncertain estimate nor a secondary result should be simplified into a categorical treatment claim.

The listed secondary measures also illustrate why trial interpretation depends on a testing plan. When numerous domains are assessed, isolated favorable results need context about prespecification and multiplicity. That context is not reported in the registry record, and numerical results are not posted for every listed secondary outcome. Statistical restraint is therefore especially important when comparing secondary findings with the primary result.

Finally, the record demonstrates the difference between a sponsor's model-based analysis and a recalculation from summary statistics. The latter can offer a useful check, but it cannot reproduce the full analysis without its specification and participant-level data. Recognizing that distinction helps readers assess what the registry can establish, what remains uncertain, and which details would be needed for a more complete independent evaluation.

19. Limitations

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

Several trial-specific details needed to evaluate the result fully are not reported in the registry record. The primary analysis is identified as a mixed-model analysis, but the model formula, covariates, repeated-measure covariance assumptions, and handling of incomplete observations are not given. The full analysis set is named without a definition, and the record does not specify how participants with protocol deviations or missing assessments were treated.

The official title describes an adaptive trial, but the adaptation rules, interim analysis procedures, and whether the design changed are not reported. The original sample-size justification and its assumptions are also not reported. Planning illustrations based on the observed effect are not a substitute for those original design details.

The registry includes many outcome measures, but the multiplicity strategy and full analysis plan are not reported. Detailed numerical findings are available for only a subset of the secondary outcomes identified in the record. This limits evaluation of consistency across all planned outcomes and makes isolated secondary results harder to interpret.

The recalculated primary interval is approximate and unadjusted, using posted summaries rather than the sponsor's full model. The sponsor's interval is the appropriate reference for the reported trial analysis, but insufficient model detail prevents independent reproduction from the registry record. The registry also does not state a clinically important difference for the CGI-S A/A scale, limiting assessment of the practical importance of the estimated score change.

Finally, adverse-event counts are descriptive and do not include enough detail to establish causality, event timing, or comparative risk over a common follow-up duration. These limitations define what can be concluded from the registry record; they do not establish that unreported procedures were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Test the Efficacy and Safety of Vafidemstat in Adult Borderline Personality Disorder Population — NCT04932291.
• Registry record last updated 2026-05-05; status last verified 2025-02.
• Results first posted 2026-05-05.
• 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

PORTICO is a completed randomized, double-blind, parallel-group Phase IIb trial of vafidemstat 1.2 mg versus placebo in adults with BPD. The registry reports enrollment of 211 and identifies change in CGI-S A/A from baseline to the average of Weeks 8 to 12 as the primary outcome.

The sponsor-reported primary mixed-model estimate is -0.16, with a 95% confidence interval from -0.42 to 0.1 and p=0.227. The interval spans zero, leaving the average between-arm difference uncertain. The registry lists secondary symptom and clinical measures, but detailed results, multiplicity procedures, missing-data methods, and important aspects of the adaptive design are not fully reported.