A Study of Aticaprant as Adjunctive Therapy in Adult Participants With Major Depressive Disorder (MDD) With Moderate-to-severe Anhedonia and Inadequate Response to Current Antidepressant Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Aticaprant as Adjunctive Therapy in Adult Participants With Major Depressive Disorder (MDD) With Moderate-to-severe Anhedonia and Inadequate Response to Current Antidepressant Therapy (NCT05455684), a randomized phase 3 study. The primary outcome is Change From Baseline to Day 43 in the Montgomery-Asberg Depression Rating Scale (MADRS) Total Score.

2. Clinical Question

The study addresses a specific clinical-trial question: whether adding aticaprant to an existing antidepressant regimen is associated with a different short-term change in depressive symptoms than adding placebo in adults selected for moderate-to-severe anhedonia and an inadequate response to current treatment. The comparison is between treatment strategies on top of continuing SSRI or SNRI therapy, not between aticaprant and no antidepressant treatment.

The primary outcome was change in MADRS total score from Baseline (Day 1) to Day 43. The registry record describes MADRS as a clinician-rated measure of depression severity. Its item content includes mood, sleep, appetite, concentration, energy, ability to feel, pessimistic thoughts, and suicidal thoughts. Higher total scores indicate more severe symptoms; a negative change indicates improvement.

The study was randomized, double-blind, parallel-group, and placebo-controlled. Those design features frame the intended comparison, but they do not by themselves establish that the observed difference is precise or that it is attributable to a treatment effect. The result must be read alongside its confidence interval, the sponsor's repeated-measures analysis, the definition of the analysis population, and the limits of the posted record.

The registry record does not report the participant-level symptom histories or the clinical reasons for each participant's inadequate response. It also does not report broader effectiveness beyond the recorded outcomes and follow-up. The question answered by the posted primary result is therefore narrow: the estimated between-group difference in change on MADRS through Day 43 in the stated analysis population.

3. Trial Design

This was a Phase 3, randomized, double-blind, multicenter, parallel-group, placebo-controlled study of aticaprant as adjunctive therapy. The registry record lists an enrollment of 513 and marks the study completed. The listed start date is 2022-06-22 and the primary completion date is 2024-09-18. These record dates describe the study timeline; they do not establish the timing of every analysis or data-cleaning decision.

Participants had major depressive disorder with moderate-to-severe anhedonia and an inadequate response to current antidepressant therapy with an SSRI or SNRI. The intervention was aticaprant 10 mg alongside ongoing antidepressant therapy; the comparator was matching placebo alongside that therapy. The arm descriptions specify once-daily oral administration during a 42-day double-blind treatment phase. The intervention descriptions also mention possible participation in a separate longer follow-up study for those who completed treatment, but the complete arm descriptions are truncated in the registry record, so further details are not reported in the registry record.

Random assignment is intended to make treatment groups comparable on average, while double blinding and a matching placebo are intended to limit some sources of bias. The registry record does not report the randomization sequence method, allocation concealment procedures, the exact blinding roles, or whether blinding was assessed. These implementation details should not be inferred from the design labels alone.

The primary endpoint was evaluated from Baseline (Day 1) to Day 43. The primary analysis population is described as the full analysis set, including randomized adults with MDD and moderate-to-severe anhedonia who received at least one dose and were evaluable for this outcome. The outcome-specific analyzed counts are listed by arm in the posted results; these are not interchangeable with enrollment or with the safety populations.

The registry record identifies a Mixed Model for Repeated Measures for the reported primary comparison. It does not report the model's complete specification, covariates, covariance structure, handling of intercurrent events, or missing-data assumptions. The original sample-size justification and design assumptions are not reported in the registry record. The planning illustrations based on observed effects are separate from the study's original design rationale.

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: Adult participants aged 18 to 64 years who had major depressive disorder (MDD) with or without moderate-to-severe anhedonia (ANH+ or ANH-) and elderly participants aged 65 to 74 years with MDD (ANH+ and ANH-) who had an inadequate response to an ongoing antidepressant therapy were randomized in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (ANH+) included all adult randomized participants with MDD ANH+ who received at least 1 dose of study intervention. Here, 'N' (overall number of participants analyzed) signifies number of participants evaluable for this outcome measure.

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 analysis set included all randomized participants (adults and elderly) who took at least 1 dose of study intervention.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Day 43 in the Montgomery-Asberg Depression Rating Scale (MADRS) Total Score, measured over Baseline (Day 1) to Day 43.

The primary endpoint is change from baseline to Day 43 in MADRS total score. MADRS is a clinician-rated measure intended to quantify depression severity and detect changes during antidepressant treatment. It contains 10 items, each scored from 0 to 6, with the total spanning 0 to 60. Higher scores indicate more severe symptoms; negative change from baseline indicates improvement.

The scale covers several aspects of depressive symptoms, including apparent and reported sadness, inner tension, sleep, appetite, concentration, lassitude, ability to feel, pessimistic thoughts, and suicidal thoughts. A total score offers a single summary measure for comparing the average symptom trajectory between randomized groups. It does not show which individual symptoms account for a change, and the group mean does not describe every participant's experience.

The endpoint is expressed as least-squares mean change, and the posted arm-level uncertainty measure is a standard error. A least-squares mean is a model-based estimate rather than a simple raw average; the exact model specification is not reported in the registry record. The reported primary contrast is the least-squares mean difference between aticaprant and placebo, with a confidence interval and p-value from the sponsor's Mixed Model for Repeated Measures analysis.

Day 43 is the specified endpoint time point for this comparison. The result therefore concerns the average change over the recorded treatment period, rather than persistence after treatment or longer-term outcomes. The registry record does not report a threshold for a clinically important between-group difference, so the numerical contrast alone cannot establish how clinically meaningful a difference would be.

7. Results Posted in the Registry

• Aticaprant 10 mg: mean -12.30 versus -11.40 on control; difference -0.90 (95% CI -3.58 to 1.78), standardized effect d = -0.07; z-test p = 0.510.

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.

Change From Baseline to Day 43 in Dimensional Anhedonia Rating Scale (DARS) Total Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Aticaprant 10 mg: mean 12.00 versus 10.50 on control; difference 1.50 (95% CI -2.56 to 5.56), standardized effect d = 0.09; z-test p = 0.469.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aticaprant 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Achieved Response on Depressive Symptoms Scale Based on MADRS Total Score at Day 43

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Aticaprant 10 mg: 29.4% (50/170) versus 22.8% (38/167) on control; risk difference 6.7 percentage points (95% CI -2.7 to 16.0), risk ratio 1.29 (0.90–1.86); unadjusted two-proportion z-test p = 0.164.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aticaprant 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Remission of Depressive Symptoms Based on MADRS Total Score at Day 43

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Aticaprant 10 mg: 17.6% (30/170) versus 12.6% (21/167) on control; risk difference 5.1 percentage points (95% CI -2.6 to 12.7), risk ratio 1.40 (0.84–2.35); unadjusted two-proportion z-test p = 0.194.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aticaprant 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context about anhedonia, depressive symptoms, and symptom response or remission. Their estimated directions are not all expressed on the same scale, so they should not be collapsed into a single overall effect. They complement the primary MADRS comparison but do not replace it: the primary result remains the planned comparison of MADRS change through Day 43, while the secondary outcomes address related but distinct questions.

The posted secondary summaries show a numerically higher DARS change estimate and higher response and remission percentages in the aticaprant group than in the placebo group. The simple recalculated intervals for these contrasts include their no-difference values. The registry record does not include sponsor-reported model analyses for these posted secondary outcomes. Thus, the observed directional pattern is descriptive and does not establish that the secondary outcomes differ reliably between groups.

Secondary outcomes often help assess whether a primary result is accompanied by changes in related constructs. DARS measures anhedonia, while response and remission classify depressive symptoms using MADRS criteria; they are related to the primary measure but are not equivalent to a continuous change score. Their different measurement forms and analysis populations also mean that direct numerical comparison is not appropriate.

Unadjusted secondary p-values, where recalculations are available, carry less inferential weight when multiple outcomes are examined. Without a reported multiplicity strategy, the chance of obtaining at least one nominally notable result across a family of tests is not controlled by looking at each comparison separately. The registry record does not report a testing hierarchy or multiplicity adjustment for these outcomes. Secondary findings should therefore be read as supportive or hypothesis-generating context, not as independent confirmation of the primary comparison.

The record lists additional secondary outcomes, including change over time in MADRS and DARS, PHQ-9 measures, and the PHQ-9 anhedonia item. Not all listed outcomes have result details in the posted secondary data used for these comparisons. Their results, multiplicity handling, and interpretation are not reported in the registry record. No broader claim about consistency across every secondary outcome can be made from the results described.

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

• Change From Baseline to Day 43 in Dimensional Anhedonia Rating Scale (DARS) Total Score
• Change From Baseline Over Time in MADRS Total Score
• Percentage of Participants Who Achieved Response on Depressive Symptoms Scale Based on MADRS Total Score at Day 43
• Percentage of Participants With Remission of Depressive Symptoms Based on MADRS Total Score at Day 43
• Change From Baseline to Day 43 in Patient Health Questionnaire, 9-Item (PHQ-9) Total Score
• Change From Baseline Over Time in DARS Total Score
• Change From Baseline Over Time in the PHQ-9 Anhedonia-specific Item (PHQ-9, Item 1)
• Percentage of Participants With a Score Less Than (<) 2 in the PHQ-9 Anhedonia-specific Item (PHQ-9, Item 1) at Day 43

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score measured on a numerical scale, and the analysis compares average change between groups. The posted arm estimates are least-squares means, accompanied by standard errors. A standard error describes the sampling uncertainty of an estimated mean; it is not the spread of individual participant scores. The sponsor's reported contrast is a least-squares mean difference from a Mixed Model for Repeated Measures.

What does the repeated-measures model do?

In general, a repeated-measures model uses observations collected at multiple time points to estimate treatment-group differences while accounting for the fact that measurements from the same participant are related. Such models can use the pattern of observed outcomes across visits rather than treating each measurement as independent. The registry record names the model but does not give its full specification, the visits included, the covariance structure, or the covariates. Those details should not be assumed.

The reported primary result is a model-based least-squares mean difference of -0.9. Its 95% confidence interval is -3.24 to 1.49, and the p-value is 0.467. The confidence interval is an uncertainty range constructed by the analysis procedure: under its assumptions and repeated use, intervals made this way would cover the target parameter at the stated rate. It is not a range containing a stated proportion of individual participant outcomes, and it does not assign a probability to the fixed treatment effect after the data are observed.

How does the recalculation differ?

The recalculated primary comparison uses posted arm-level means and standard errors to obtain a simple unadjusted contrast. The recalculation reports a mean difference of -0.9, 95% confidence interval from -3.575 to 1.775, and p = 0.51. The standard deviations used in the recalculation are approximated from standard errors, as indicated in the record. This calculation does not reproduce the repeated-measures model and should not be treated as a competing primary analysis. It is a transparent summary-statistic check, whereas the sponsor's reported analysis is model-based.

Both comparisons use the placebo arm as the reference. A negative difference on MADRS points toward a greater reduction in the aticaprant group, given that negative change denotes improvement. The sign is meaningful only in conjunction with the scale's direction and the comparison order; it is not itself evidence of a reliably different result.

What do unadjusted secondary comparisons mean?

For secondary outcomes with recalculated comparisons, the record supplies unadjusted estimates and p-values. An unadjusted p-value evaluates a particular contrast without accounting for the fact that multiple outcomes may be examined. When many outcomes are tested, the chance of at least one apparently notable result can increase. Multiplicity procedures can control that issue, but a correction method or a hierarchical testing plan is not reported in the registry record. Thus, secondary comparisons should be treated as exploratory context unless a prespecified inferential plan is documented elsewhere in the record.

Continuous outcomes such as DARS use mean differences, while binary outcomes such as response and remission use percentage summaries and a risk difference. In general, a risk difference expresses the difference between two event proportions on the probability scale. The posted recalculation gives the risk difference and an interval; its interval can be compared with zero as the no-difference value. The registry record also lists relative measures for the binary endpoints, but those are not needed to understand the primary endpoint and are not a substitute for the prespecified analysis.

Approximation matters when reconstructing uncertainty from summaries. The primary recalculation derives variation from standard errors and analyzed counts rather than participant-level data; for the DARS outcome, the same type of approximation is indicated. For binary outcomes, a simple calculation relies on event counts and denominators and does not incorporate any unreported model adjustments. Such re-calculations are useful for orientation but can differ from model-based estimates because they do not have access to the same data or assumptions.

Why can over-dispersion matter?

In general, over-dispersion occurs when the observed variability in count or binary data exceeds what a simple probability model expects. If ignored, uncertainty can be understated and intervals can be too narrow. The registry record does not state that over-dispersion was present or describe a specific correction; this is a general statistical consideration, not a finding about this trial.

Likewise, missing data can affect a repeated-measures estimate if the likelihood of missingness is related to outcomes or treatment. A model may rely on assumptions about the relationship between observed and unobserved outcomes. The record does not report the missing-data pattern, sensitivity analyses, or assumptions used in the sponsor analysis. The reported estimate should therefore be interpreted with that documentation gap in mind.

Finally, statistical significance and clinical importance are different concepts. A p-value addresses compatibility with a specified statistical null under model assumptions; a confidence interval conveys uncertainty about the magnitude and direction. Clinical importance requires context, including a meaningful-difference threshold and patient-centered interpretation. Such a threshold is not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor's primary estimate is a least-squares mean difference of -0.9 MADRS units, with a 95% confidence interval from -3.24 to 1.49. The interval crosses zero, the value corresponding to no between-group difference. It includes estimates favoring a larger reduction with aticaprant and estimates favoring a larger reduction with placebo. The point estimate alone does not resolve that uncertainty.

In general, a confidence interval describes the precision of an estimate under the statistical model used to calculate it. A narrower interval indicates greater precision than a wider interval on the same scale; an interval crossing the no-difference value indicates that the data do not pin the contrast to one direction at that confidence level. The interval does not mean that there is a 95% probability that the fixed true effect lies inside these particular endpoints.

The simple unadjusted recalculation gives a 95% confidence interval from -3.575 to 1.775. It is wider than the sponsor interval and also crosses zero. The two intervals should not be treated as interchangeable: the sponsor result comes from a Mixed Model for Repeated Measures, while the recalculation uses arm-level summary statistics and approximated variation. Their shared broad feature is uncertainty spanning zero, not identical precision or modeling assumptions.

The arm-specific standard errors were 0.98 for placebo and 0.95 for aticaprant. These describe uncertainty in the estimated arm means, not the variability of individual MADRS scores. The recalculation uses an approximated pooled standard deviation of 12.07 and an effect-size estimate of -0.075; these are derived summaries, not separate trial outcomes.

Precision is also limited by the analysis population and the outcome-specific evaluable counts. The primary outcome counts are 155 for placebo and 158 for aticaprant. The registry record does not report the pattern or reasons for missing outcome data, nor sensitivity analyses for missingness. A confidence interval cannot account for bias caused by assumptions that do not hold. The interval is therefore one component of uncertainty, alongside data completeness and the model specification that is not fully documented 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 illustrations translate an observed contrast into hypothetical planning requirements. For these continuous and binary outcomes, the displayed quantities are participants per arm, not total participants and not total events. The planning assumptions listed are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would give an 80% chance of rejecting the statistical null under the assumed effect and model. The 90% power column describes the corresponding planning requirement for a 90% chance. Power is conditional on the assumed effect and analysis conditions; it is not a guarantee that a future study will reach a particular result.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more participants for a given target power, because a subtler contrast is harder to distinguish from sampling variation. In the primary endpoint illustration, the estimates are especially sensitive to the small observed effect. The values are planning illustrations, not a report of the original trial's target enrollment or sample-size justification. The original design assumptions are not reported in the registry record.

These figures are not observed power. Observed power calculated from the trial's own estimated effect would largely restate the result's uncertainty and does not provide an additional measure of evidence. The planning exercise is more useful when treated as a conditional question: if a future study aimed to detect an effect of the specified fraction under the listed assumptions, what participant count per arm would the calculation suggest?

The assumptions simplify actual trial planning. The registry record does not describe allowance for attrition, alternative allocation, covariate adjustment, multiplicity, or departures from the normal approximation in the original design. The illustrations should not be used as a substitute for a protocol-based design calculation.

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 = -0.900; pooled standard deviation σ = 12.071.
2. n = 2 × (1.96 + 0.842)² × 12.071² / -0.900² = 2,823.6, rounded up to 2,824 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 <- -0.9                      # observed difference in means
sigma <- 12.0705539770094                     # 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(5455684)
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 = 2,824 (80% power), 3,781 (90% power)
 75% of observed effect: n per arm = 5,020 (80% power), 6,721 (90% power)
 50% of observed effect: n per arm = 11,295 (80% power), 15,121 (90% power)
power.t.test: 2824.6 
Simulated power at n = 2,824 per arm: 0.795 (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 reported primary analysis is a Mixed Model for Repeated Measures and gives a least-squares mean difference of -0.9, with a 95% confidence interval from -3.24 to 1.49 and p = 0.467. This is the model-based analysis reported in the registry record and is the appropriate result to foreground when describing the primary comparison.

The simple recalculation from the posted arm summaries gives the same point estimate, -0.9, but a 95% confidence interval from -3.575 to 1.775 and p = 0.51. It is unadjusted and uses approximate variation reconstructed from summary statistics. It does not reproduce the sponsor's repeated-measures model, and small differences in intervals and p-values are expected when methods and available information differ.

The registry record does not flag a discrepancy between the sponsor result and the recalculation. Their statistical conclusions are similar in the limited sense that each interval includes zero. That does not make the approaches identical, and the recalculation should not override the sponsor's model-based estimate. The record does not provide enough model detail to independently reproduce the sponsor analysis from participant-level data.

The sponsor analysis concerns the stated primary endpoint and analysis population. It should not be extended to outcomes, time points, or populations that were not part of that analysis. The precision and interpretive limits of the reported estimate remain important regardless of which calculation is being described.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or statistical contrasts are evaluated. Even if each test uses the same nominal significance threshold, conducting many tests increases the opportunity for at least one result to appear notable by chance. Common approaches include defining a primary outcome, setting a hierarchy for testing, or adjusting significance thresholds or intervals. Which approach is appropriate depends on the design and inferential goal.

The registry record identifies a primary outcome and lists secondary outcomes, but a formal multiplicity procedure or hierarchical testing plan is not reported in the registry record. The posted secondary recalculations are unadjusted. Their p-values should not be interpreted as if they accounted for all outcome comparisons. The primary result remains the most direct test of the stated main question; secondary results are less conclusive when no adjustment strategy is documented.

Missing-data information is also limited. The primary analysis population includes randomized participants who received at least one dose and were evaluable for the outcome. The registry record does not report how many outcome observations were missing at each visit, why they were missing, how missing data were handled in the sponsor model, or whether sensitivity analyses assessed departures from the model's assumptions. Those details matter because the estimate can be affected if missingness is related to symptoms, treatment, or tolerability.

The Mixed Model for Repeated Measures is named, but its full specification and assumptions are not reported in the registry record. In general, repeated-measures analyses can rely on assumptions about the relation between observed and missing outcomes; the record does not establish which assumptions were used or whether they were tested. It would be inappropriate to infer a particular missing-data method from the model label alone.

The full analysis set is described for the primary endpoint, while outcome-specific analyzed counts differ across endpoints. The record defines the primary population but does not provide a full account of all analysis populations for every secondary outcome. The relation between randomized, treated, evaluable, and safety populations should therefore be kept clear. The registry record also does not report protocol deviations or exclusions in sufficient detail to assess their possible impact.

These documentation gaps do not invalidate the posted estimates, but they limit independent appraisal of the analysis choices and robustness. They are reasons to interpret secondary findings and model-dependent precision cautiously, rather than reasons to assume a particular bias or direction of effect.

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: pancreatitis acute (0.4%), suicidal behaviour (0.4%), asthma (0.4%), pneumonia (0.4%).

The registry safety figures distinguish serious adverse events from other adverse events and list double-blind and follow-up groups separately. During the double-blind period, the serious adverse event count was 1 among 258 at risk in the placebo group and 3 among 253 at risk in the aticaprant 10 mg group. The record lists zero deaths in each of those groups.

For follow-up, the registry lists zero serious adverse events among 24 at risk in the placebo group and zero among 14 at risk in the aticaprant group. Deaths are also listed as zero in these follow-up groups. The other adverse event counts during the double-blind period were 34 in the placebo group and 54 in the aticaprant group; the follow-up counts were zero and 1, respectively. These figures are counts as recorded, not adjusted comparisons of risk.

The serious-event terms listed at 0.4% each are Pancreatitis Acute, Suicidal Behaviour, Asthma, and Pneumonia. The registry record does not provide enough detail in these summaries to establish event timing, relatedness to study intervention, recurrence, severity beyond the serious classification, or comparative risk estimates for each term.

Safety denominators differ from the primary outcome analysis counts and should not be substituted for them. Event counts alone do not establish causation, and uncommon events can be imprecisely characterized in a trial record. These data describe reported events in the listed groups and do not by themselves establish a comprehensive safety profile.

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

The primary result is an estimate of the difference between adjunctive aticaprant and adjunctive placebo in change on a clinician-rated depression scale through Day 43, in adults with major depressive disorder, moderate-to-severe anhedonia, and inadequate response to current SSRI or SNRI therapy. It is not a comparison of aticaprant with no treatment, because participants continued background antidepressant therapy in both groups.

The posted arm estimates show negative MADRS change in both groups, consistent with improvement on the scale. The aticaprant point estimate is more negative, and the estimated between-group difference is -0.9. But the sponsor's 95% confidence interval, -3.24 to 1.49, includes zero. The data therefore do not identify a precise direction for the between-group contrast at that confidence level. The result should not be translated into a categorical statement that the adjunctive treatment works or does not work.

The endpoint is a group-level summary. It does not mean that every participant improved, that participants changed by the average amount, or that the same symptom domains changed for all participants. Response and remission are separate secondary classifications and do not substitute for individual-level interpretation of the primary mean change.

The findings apply to the recorded treatment period and eligible population. They do not establish longer-term effects, effects in other populations, or effects with background treatments outside the stated SSRI/SNRI context. The registry record does not report a clinically important difference threshold, so statistical uncertainty cannot be converted directly into a judgment about clinical importance.

Interpretation also depends on analysis assumptions and data completeness. The sponsor model is named but not fully specified, and missing-data patterns and sensitivity analyses are not reported in the registry record. Those omissions limit independent assessment of robustness. The secondary results are likewise limited by the lack of reported multiplicity handling and sponsor analyses for the listed comparisons.

In short, the posted evidence is a short-term, model-based estimate with uncertainty spanning no difference. It supports a careful description of the observed scores and their precision, not a definitive treatment recommendation or a claim beyond the trial's recorded population, outcome, and time point.

18. Why This Trial Matters Statistically

This study is statistically informative because its question concerns an adjunctive strategy in a defined population rather than an isolated treatment in an unrestricted group. Continuing background SSRI or SNRI therapy in both arms makes the contrast relevant to added therapy, while also defining the limits of what the comparison can answer.

The primary result illustrates why effect estimates and uncertainty should be read together. The point estimate is not the whole result: the confidence interval spans zero and extends in both directions. A single directionally favorable point estimate is not enough to determine whether groups differ reliably, and a non-small p-value is not proof that there is no meaningful effect. The interval communicates the range of values compatible with the model and data more directly than a binary significant/not-significant label.

The record also demonstrates the distinction between a sponsor's prespecified model-based comparison and a simple recalculation from posted arm summaries. The recalculation can provide a transparent check, but it cannot reconstruct all features of the repeated-measures analysis. Reporting both as different statistical objects helps prevent a summary-data approximation from being mistaken for a replication of the primary analysis.

Secondary endpoints matter because anhedonia and depressive symptoms overlap but are not identical constructs. Their interpretation nevertheless depends on a coherent testing strategy. Without a reported multiplicity procedure, a set of secondary contrasts should not be treated as multiple independent confirmations. The results illustrate the need to report the planned hierarchy, missing-data approach, and analysis details alongside estimates.

Finally, planning illustrations based on observed effects highlight the difficulty of designing studies around small contrasts, but they do not explain the original trial design. Separating such illustrations from actual design assumptions is important for sound statistical interpretation. The registry record supports careful appraisal of the posted estimate while leaving meaningful questions about analysis specification and data completeness unanswered.

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 registry record does not fully specify the sponsor's repeated-measures model. The model name is reported, but covariates, covariance structure, time-point specification, and treatment of intercurrent events are not. This restricts independent reproduction and makes it difficult to assess how model choices affected the estimate.

Missing-data details are not reported in the registry record. There is no posted account of missing assessments by visit and arm, reasons for missingness, the assumptions used for unobserved outcomes, or sensitivity analyses. Because the primary result relies on a repeated-measures model, these details are relevant to how confidently its interval can be interpreted.

The primary endpoint analysis includes participants who received at least one dose and were evaluable for the outcome. This is not identical by definition to all randomized participants. The registry record does not provide enough detail to assess the consequences of exclusions, protocol deviations, or differences among analysis populations.

The study's stated population is specific: adults with MDD, moderate-to-severe anhedonia, and inadequate response to current SSRI or SNRI therapy. Generalization beyond that context is uncertain. The primary time point is Day 43, so the result does not establish durability. The record mentions a separate longer follow-up study in truncated arm descriptions, but detailed follow-up design and outcomes are not reported in the registry record.

Multiplicity handling for secondary outcomes is not reported. The recalculated secondary comparisons are unadjusted, and sponsor analyses are not posted for the secondary outcomes summarized. These results therefore have less inferential weight than the primary comparison.

The recalculations are based on aggregate summaries and, for continuous measures, approximated variation. They cannot reproduce participant-level analyses or account for model adjustments not present in the summaries. The registry record also does not report a clinically important difference threshold for MADRS, which limits interpretation of the magnitude in clinical terms.

Safety summaries provide event counts and at-risk denominators, but they do not establish causality or provide detailed event-level context. The figures should be read as registry-reported safety observations rather than a complete comparative safety assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Aticaprant as Adjunctive Therapy in Adult Participants With Major Depressive Disorder (MDD) With Moderate-to-severe Anhedonia and Inadequate Response to Current Antidepressant Therapy — NCT05455684.
• Registry record last updated 2025-11-06; status last verified 2025-10.
• Results first posted 2025-11-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, double-blind, parallel-group, placebo-controlled Phase 3 study of aticaprant 10 mg as adjunctive therapy in adults with major depressive disorder, moderate-to-severe anhedonia, and inadequate response to SSRI or SNRI therapy. The primary outcome was MADRS change from Baseline (Day 1) to Day 43.

The sponsor's reported primary comparison was a Mixed Model for Repeated Measures least-squares mean difference of -0.9, with a 95% confidence interval from -3.24 to 1.49 and p = 0.467. The interval includes zero. A simple unadjusted recalculation from posted summaries gives the same point estimate with a wider interval, also spanning zero.

Secondary outcomes provide related symptom and anhedonia measures, but unadjusted results and undocumented multiplicity handling limit their confirmatory weight. Serious adverse event counts are listed separately for double-blind and follow-up groups. The registry record does not report full model details, missing-data sensitivity analyses, or the original sample-size justification.