Clinical Trial Evaluating Lumateperone Monotherapy in the Treatment of Bipolar Depression or Major Depressive Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial Evaluating Lumateperone Monotherapy in the Treatment of Bipolar Depression or Major Depressive Disorder (NCT04285515), a randomized phase 3 study. The primary outcome is Change From Baseline in Montgomery-Åsberg Depression Rating Scale (MADRS) Total Score.

2. Clinical Question

3. Trial Design

NCT04285515 is a Phase 3, randomized, quadruple-masked, parallel-group trial sponsored by Intra-Cellular Therapies, Inc. The registry lists an enrollment of 488 and status as completed. The listed start date is 2020-02-27, and the primary completion date is 2022-11-30. These registry entries describe the study record; the primary outcome analysis has its own reported group sizes.

The study compared lumateperone monotherapy with matching placebo. Lumateperone 42mg and placebo were each administered once daily in the evening. The brief description identifies a screening period, a double-blind treatment period, and a safety follow-up period. It describes the intended population as patients with major depressive episodes associated with Bipolar I or Bipolar II disorder, or major depressive disorder, who also meet DSM-5 criteria for mixed-features.

The primary endpoint was change from baseline in MADRS total score at Day 43 for the combined MDD and Bipolar Depression Mixed Features Population. The registry identifies the primary outcome estimate as a least-squares mean and its dispersion as a standard error. Its reported analysis uses a Mixed Effects Model for Repeated Measure and gives a least-squares mean difference between the groups.

Registry enrollment and outcome-analysis group sizes are different record details and should not be treated as interchangeable. The record does not report the original sample-size justification, the full protocol, detailed eligibility criteria, or the full statistical analysis plan. It also does not report how many participants completed treatment or the specific analysis populations used for each outcome.

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: Combined MDD and Bipolar Depression Mixed Features Population

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Montgomery-Åsberg Depression Rating Scale (MADRS) Total Score, measured over Day 43.

The primary endpoint is change from baseline in total score on the Montgomery-Åsberg Depression Rating Scale (MADRS) at Day 43. The registry describes MADRS as a clinician-rated, 10-item scale for assessing depressive symptoms. Each item is rated on a 7-point scale from 0-6; the total score ranges from 0 to 60, with higher scores indicating greater severity of depressive symptoms.

A change-from-baseline endpoint compares each participant’s score at follow-up with that participant’s starting score, then summarizes those changes by treatment group. This makes the endpoint a measure of change during the treatment period rather than simply a comparison of scores at one time point. In the posted primary outcome, the group summaries are least-squares means, which are model-based estimates rather than necessarily raw arithmetic averages.

In general, a symptom rating scale can provide a standardized way to quantify changes in a clinical domain. The interpretation still depends on the scale, the population, the timing of measurement, and the analysis used. The registry reports the endpoint at Day 43; it does not report additional context about the clinical importance threshold for a MADRS change or the criteria used to define a meaningful individual response.

7. Results Posted in the Registry

• Lumateperone 42mg: mean -18.10 versus -12.40 on control; difference -5.70 (95% CI -7.65 to -3.75), standardized effect d = -0.58; z-test p = <0.001.

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.

Clinical From Baseline in Clinical Global Impression Scale - Severity (CGI-S)

• 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:
  • Lumateperone 42mg: mean -1.80 versus -1.20 on control; difference -0.60 (95% CI -0.82 to -0.38), standardized effect d = -0.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Lumateperone 42mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists four secondary outcomes as posted, while the numerical secondary result described in the record is change from baseline in Clinical Global Impression Scale - Severity (CGI-S) at Day 43. Its reported model-based contrast is negative, in the same direction as the primary MADRS contrast. This directional agreement is a limited observation about the reported outcomes; it does not show that every secondary endpoint had a similar result.

The registry record does not report numerical results for the other secondary outcomes in the registry record used for this analysis. As a result, a complete pattern across all posted secondary endpoints cannot be assessed from this record. The listed secondary-outcome count should not be treated as evidence that all outcomes were statistically significant, consistent, or analyzed using the same method.

Secondary outcomes can add context by assessing related aspects of a trial, but they generally carry less inferential weight than the designated primary outcome. In general, testing multiple outcomes creates more opportunities for apparently notable results to occur by chance unless a suitable multiplicity strategy is planned and applied. The registry record does not report whether secondary comparisons were adjusted for multiplicity or how their inferential status was defined.

Accordingly, the CGI-S result may be described as a secondary finding aligned in direction with the primary result, while keeping the primary MADRS analysis central. The missing numerical results and unreported multiplicity procedure limit any broader claim about consistency across secondary endpoints.

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

• Clinical From Baseline in Clinical Global Impression Scale - Severity (CGI-S)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric scale score, and the registry reports group means as least-squares means. The primary analysis is identified as a Mixed Effects Model for Repeated Measure, with the treatment contrast expressed as a least-squares mean difference. This is the sponsor-reported inferential result in the registry. The exact model specification, including its covariates and covariance structure, is not reported in the registry record.

What does a least-squares mean represent?

In general, a least-squares mean is an estimate derived from a statistical model. Unlike a simple raw average, it can reflect the model’s structure and any included adjustment variables. The associated difference compares the model-based group estimates on the outcome’s scale. Here, the reported primary estimate is -5.7 points for the lumateperone-versus-placebo comparison. The registry does not report enough model detail to reproduce the adjusted estimate independently from the group summaries.

What does a repeated-measures model do?

In general, repeated-measures methods are designed for outcomes measured over time, where multiple measurements from the same participant are related rather than independent. A mixed-effects model can represent this within-participant correlation while estimating group differences. The registry names a repeated-measures model for the primary outcome, but does not report its full specification, the number or timing of all measurements included in the model, or the assumptions used for the analysis.

The primary endpoint is stated as change from baseline at Day 43. The registry reports outcome group sizes of 192 for lumateperone and 191 for placebo. These are the sizes attached to the posted primary outcome summaries; the enrollment entry is a separate trial-record figure. The record does not specify the exact analysis population definition or explain whether all randomized participants contributed to the model.

How should the recalculation be understood?

The posted recalculation is an unadjusted comparison based on the outcome summaries. It gives a mean difference of -5.7, with an approximate 95% confidence interval from -7.654 to -3.746 and p <0.001. Its pooled standard deviation is marked as approximate. This calculation offers a simple summary-based reference, but it does not reproduce the sponsor’s repeated-measures model. The model-based result reported by the sponsor should be used as the trial’s principal analysis.

In general, a standard error describes the sampling uncertainty of an estimate. The primary group summaries report standard errors of 0.71 and 0.7. A standard error is not the spread of individual participant scores; it describes uncertainty in the estimated group mean. The registry does not provide the individual-level outcome data needed to examine score distributions, outliers, or model diagnostics.

What does the p-value test?

In general, a p-value evaluates how compatible the observed data are with a specified null hypothesis under the statistical model. The reported primary p-value is < 0.001. This is evidence against the null hypothesis used for the reported test, but it is not a measure of effect size or clinical importance. The estimated difference and its confidence interval provide information about the magnitude and precision of the result. The registry’s summary recalculation gives p <0.001; that unadjusted value is not the same as the sponsor’s model-based test.

The registry classifies the primary comparison as superiority. This label describes the direction and inferential framework of the reported comparison; it does not reveal every decision rule in the analysis plan. Details about the planned hypothesis, significance threshold for the sponsor analysis, multiplicity adjustment, model diagnostics, and handling of missing values are not reported in the registry record.

For the secondary CGI-S outcome, the registry names a Mixed Effects Model of Repeated Measure and reports a least-squares mean difference. In general, using a similar model framework for another repeated clinical measure can make the estimated contrast interpretable on that measure’s own scale. The CGI-S estimate and its uncertainty are specific to CGI-S and should not be interpreted as MADRS points.

Overall, the reported model-based estimates should be distinguished from summary-based recalculations. The latter rely on posted group statistics and are useful as approximate, unadjusted checks. They cannot account for model features that are not represented in those summaries. No details on interim analyses, the original statistical plan, missing-data handling, or adjustments across multiple outcomes are reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is -5.7, with a 95% confidence interval from -7.60 to -3.84. In general, a confidence interval expresses the uncertainty associated with an estimate under the statistical method used. It gives a range of values compatible with the data and model at the stated confidence level; it is not a guarantee that the true value lies in that particular interval.

Both reported limits are below zero, so the sponsor’s interval is consistent with a negative group difference under the model. The interval still spans multiple possible effect sizes, which means the exact magnitude is uncertain. The registry’s unadjusted recalculation gives an approximate interval from -7.654 to -3.746. Because it is based on posted summary statistics and an approximate pooled standard deviation, it should not be treated as the same interval as the model-based sponsor result.

The secondary CGI-S model-based estimate is -0.6, with a 95% confidence interval from -0.81 to -0.39. That interval is on the CGI-S scale and should not be compared numerically with the MADRS interval as if the measures shared a scale.

Confidence intervals describe statistical precision, not clinical importance. The registry record does not report a threshold for a clinically important difference on MADRS, nor does it report information sufficient to judge how the estimated group difference relates to individual-level variation. Precision should therefore be read alongside the outcome definition, analysis population, and limitations in the registry record.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The registry record does not report the original sample-size justification. For these illustrations, the stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

For a continuous outcome, the listed figures are participants per arm, not total participants and not total events. The rows describe planning for 100%, 75%, or 50% of the observed effect. The 80% power column gives the estimated participants per arm for an illustrative design with an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column gives the corresponding estimate for a 90% chance. Power is a design probability under specified assumptions, not a measure of certainty about the trial result.

The displayed planning figures are 46 and 62 participants per arm for 100% of the observed effect; 82 and 110 for 75%; and 184 and 247 for 50%, for the 80% and 90% power columns respectively. Smaller target effects require more participants per arm to maintain the stated power, because a smaller group difference is harder to distinguish from sampling variation.

These values are not observed power for this completed trial. They are illustrations using the observed effect as a planning reference, and should not be read as evidence that a future study with those sizes would necessarily reproduce the result. The original design rationale, any allowances for loss to follow-up, and the sponsor’s planned power calculation are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -5.700; pooled standard deviation σ = 9.757.
2. n = 2 × (1.96 + 0.842)² × 9.757² / -5.700² = 46.0, rounded up to 46 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -5.7                      # observed difference in means
sigma <- 9.75667954790588                     # 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(4285515)
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 = 46 (80% power), 62 (90% power)
 75% of observed effect: n per arm = 82 (80% power), 110 (90% power)
 50% of observed effect: n per arm = 184 (80% power), 247 (90% power)
power.t.test: 47 
Simulated power at n = 46 per arm: 0.786 (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 the Mixed Effects Model for Repeated Measure. It reports a least-squares mean difference of -5.7, a 95% confidence interval from -7.60 to -3.84, and p < 0.001. This is the trial’s reported model-based analysis and is the result to prioritize when describing the primary endpoint.

The recalculation uses posted group summaries rather than the repeated-measures model. It gives a mean difference of -5.7, an approximate 95% confidence interval from -7.654 to -3.746, and p <0.001. The recalculated pooled standard deviation is marked as approximate. Summary-based calculations cannot reconstruct model details that are not included in the posted group statistics, so differences in interval limits and p-value reporting should be understood in light of the different methods.

The registry does not flag a discrepancy between the sponsor analysis and the recalculation. Even so, the recalculation is not a substitute for the sponsor’s specified model result: it is an unadjusted approximation based on aggregate summaries. The sponsor’s own analysis remains the primary source for the trial’s reported inferential conclusion.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, time points, or subgroups are tested. In general, as the number of statistical tests increases, the chance of obtaining at least one result that appears statistically notable by chance can also increase. A prespecified plan can address this issue by defining which outcome is primary and whether and how testing across additional outcomes will be adjusted.

The registry identifies a primary MADRS endpoint and lists four secondary outcomes as posted. The numerical secondary outcome described in the record is CGI-S. The multiplicity strategy for the primary and secondary analyses is not reported in the registry record. It is therefore not possible to determine from these registry entries whether secondary p-values were adjusted, whether a testing hierarchy was used, or what confirmatory status was assigned to each secondary result.

The registry also does not report the full statistical analysis plan, details of the analysis populations, or how missing outcome data were handled. In general, repeated-measures models can use available measurements under specified assumptions, but the model name alone does not establish which missing-data assumptions were made or whether sensitivity analyses were conducted. The record does not provide enough information to assess these choices.

Other potentially important analysis details, including the model’s covariates, covariance structure, and diagnostic checks, are not reported in the registry record. The registry entries do not report interim analyses or the original sample-size justification either. These omissions do not alter the numerical estimates as posted, but they limit independent evaluation of the analysis choices and of how robust the findings may be to alternative assumptions.

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: dermatitis (0.4%).

The registry reports serious adverse events for 0 participants in the lumateperone group and 1 participant in the placebo group. The listed top serious-event term is dermatitis, at 0.4%. No deaths are reported in either group. These are safety counts recorded in the registry and should be read as descriptive figures for the trial record.

The record also reports 84 affected in the lumateperone group and 37 in the placebo group in the other adverse-event category. These figures are separate from the serious adverse-event counts. The registry entries do not provide event-level descriptions or the full safety-analysis context needed to determine how each event was classified, its duration, or its relationship to treatment.

Safety counts alone do not establish a comparative risk estimate or explain the clinical significance of individual events. The posted figures should not be taken as a complete accounting of all possible harms or as a basis for conclusions beyond the trial record.

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

The primary result describes a statistical difference between the randomized groups in mean change from baseline in MADRS total score at Day 43. The reported model-based estimate is -5.7, with a 95% confidence interval from -7.60 to -3.84 and p < 0.001. Since higher scores on MADRS indicate greater depressive symptom severity, the negative estimate corresponds to a larger mean decrease in score in the lumateperone group than in the placebo group under the analysis reported.

This result does not by itself tell whether the difference is clinically important for every participant. The registry does not report a threshold for clinical importance, individual response distributions, or longer-term outcomes. A group mean also cannot describe the full range of individual experiences. The statistical finding should therefore be separated from judgments about what a particular score change means for a particular person.

The result applies to the trial’s stated population and analysis, including participants with major depressive episodes associated with bipolar I or bipolar II disorder or major depressive disorder and mixed-features criteria. The record does not justify extending the result to populations or circumstances not described in the trial. It also does not establish the outcome of treatment outside the study conditions.

The statistical result is not a complete benefit-harm assessment. Serious adverse-event counts and other adverse-event figures are reported, but the registry record does not provide all detail needed to characterize event timing, severity, or treatment attribution. The primary efficacy result, secondary outcome information, and safety figures answer different questions and should be interpreted separately.

Finally, the registry does not report the full statistical analysis plan, multiplicity strategy, missing-data handling, or original sample-size rationale. These gaps limit how fully the posted result can be independently evaluated, without changing what the registry reports for the primary analysis.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis method matters when a clinical endpoint is measured over time. The registry’s primary result is a least-squares mean difference from a repeated-measures model, whereas a calculation from posted group summaries is an unadjusted approximation. Those quantities can answer related questions, but they are not interchangeable: the model-based estimate incorporates the analysis structure that the summary-only calculation cannot reproduce.

The record also makes clear that statistical significance and precision are different features of a result. The reported p-value is small, while the confidence interval expresses a range of estimates compatible with the model and data. Neither alone establishes clinical importance. Interpretation requires the scale’s meaning, the population studied, and the limits of the available analysis details.

Sample-size illustrations provide another useful statistical distinction. Planning figures based on an observed effect are not the same as the trial’s original design calculation and are not observed power. The registry’s original rationale is not reported, so the planning illustration should be read only as a conditional example under stated assumptions.

Finally, the difference between the primary outcome and secondary outcomes matters for inference. The registry reports a primary MADRS analysis and a numerical CGI-S secondary result, but the broader multiplicity strategy and results for the other posted secondary outcomes are not reported in the record. This limits claims about consistency while preserving the ability to describe the primary result precisely.

19. Limitations

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

The available registry information does not include the full protocol or statistical analysis plan. In particular, it does not report detailed eligibility criteria beyond the mixed-features description, the analysis-population definitions, or the complete model specification. The outcome summaries therefore do not allow independent reproduction of the sponsor’s repeated-measures analysis.

The record does not report how missing data were handled, what assumptions were made about missing measurements, or whether sensitivity analyses were performed. It also does not report the multiplicity strategy for secondary outcomes. These omissions make it difficult to assess the robustness of the findings across plausible analysis choices or to interpret secondary p-values as confirmatory evidence.

The registry reports a primary endpoint at Day 43, but the registry entries do not provide longer-term outcome results. The numerical information available for secondary outcomes is incomplete: CGI-S is described, while results for other posted secondary outcomes are not reported in the registry record. The safety information is also limited to the stated counts and listed serious-event term; it does not supply detailed event narratives or additional context.

Finally, the registry enrollment entry, outcome-analysis group sizes, and safety-group sizes refer to different record components. The record does not explain the differences among those figures or report participant flow in detail. The trial’s original sample-size justification and design assumptions are not reported, so the separate planning illustration cannot fill that gap.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Trial Evaluating Lumateperone Monotherapy in the Treatment of Bipolar Depression or Major Depressive Disorder — NCT04285515.
• Registry record last updated 2025-03-19; status last verified 2025-03.
• Results first posted 2025-03-19.
• 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

NCT04285515 is a completed Phase 3 randomized, quadruple-masked, parallel-group trial of lumateperone 42mg once daily in the evening versus matching placebo. It enrolled patients with major depressive episodes associated with Bipolar I or Bipolar II disorder or major depressive disorder who also met DSM-5 mixed-features criteria. The primary outcome was change from baseline in MADRS total score at Day 43.

The sponsor-reported repeated-measures analysis gives a least-squares mean difference of -5.7, with a 95% confidence interval from -7.60 to -3.84 and p < 0.001. A numerical secondary CGI-S result is also reported, while results for other posted secondary outcomes and several analysis details are not reported in the registry record. The record includes limited safety counts and does not provide the full analysis plan, missing-data procedures, or multiplicity strategy.