Once-Daily Asenapine for Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Once-Daily Asenapine for Schizophrenia (NCT01549041), a randomized phase 4 study. The primary outcome is Patient Acceptance.

2. Clinical Question

3. Trial Design

The registry record describes a phase 4 randomized, parallel-group trial with no masking. It lists Duke University as the sponsor and a planned enrollment of 30. The record marks the study completed; the listed start and primary completion are 2012-04 and 2013-04. These dates do not establish how long each participant was followed. The listed intervention groups were asenapine 10 mg daily in the evening and asenapine 5 mg twice daily, administered in the morning and evening.

The primary outcome was patient acceptance at day 14. The record reports 12 participants in the once-daily group and 18 in the twice-daily group for this outcome. The record does not explain the difference between the planned enrollment and the group counts in the outcome results, or provide a participant flow account. It also does not report further details about allocation procedures, eligibility criteria, adherence, or participant characteristics.

The trial summary says investigators sought to explore patient and staff acceptance and changes in psychopathology, and hypothesized better acceptance with once-daily dosing and similar psychopathology improvements between schedules. The listed primary endpoint is patient acceptance. A secondary outcome is change in Brief Psychiatric Rating Scale (BPRS) total score from baseline to day 14. The record lists two outcome measures, but does not include a posted staff-acceptance result. The record does not report the protocol’s original statistical analysis plan or sample-size justification, so the design’s intended analysis cannot be reconstructed from the posted information alone.

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

Reasons for not completing this period:

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 Patient Acceptance, measured over At day 14.

The primary endpoint is patient acceptance at day 14, measured with a Likert scale described as ranging from 1, “Very Acceptable,” to 7, “Completely Unacceptable.” The description associates the highest category with an individual refusing further doses. This makes the score a direct report of how acceptable patients found the assigned dosing schedule, rather than a measure of symptom change or a count of doses taken. Lower scores correspond to more acceptable ratings on the stated scale.

The registry reports the mean score and standard error for each group. A group mean condenses participants’ scores into an average, while the standard error describes the estimated precision of that average. The endpoint is used because the stated research question includes whether patients accept once-daily dosing differently from twice-daily dosing. A day-14 rating gives a defined time point for comparing the groups, but it does not by itself describe acceptance over the full course of treatment or establish why a participant chose a particular rating.

The result should be interpreted within the scale’s stated anchors and the outcome counts in the registry record. Further information about how the scale was administered beyond the description, how missing day-14 scores were handled, or whether any threshold for a meaningful difference was set is not reported in the registry record.

7. Results Posted in the Registry

• Asenapine 5 mg Twice Daily: mean 3.90 versus 1.70 on control; difference 2.20 (95% CI 0.81 to 3.59), standardized effect d = 1.11; z-test p = 0.002.

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 in Brief Psychiatric Rating Scale (BPRS) 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:
  • Asenapine 5 mg Twice Daily: mean 7.72 versus 16.08 on control; difference -8.36 (95% CI -15.11 to -1.61), standardized effect d = -0.90; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Asenapine 5 mg Twice Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcome is change in BPRS total score from baseline to day 14. Its group summaries and unadjusted contrast are reported alongside the primary acceptance result, but they answer a different question: the primary endpoint concerns patients’ ratings of dosing acceptability, while BPRS concerns change in a psychopathology score. The record summary identifies interest in changes in psychopathology, but the secondary result cannot be treated as a direct confirmation of the primary endpoint.

The registry summary hypothesizes similar improvements in psychopathology across dosing schedules. Similarity is a specific claim that generally requires a defined margin and an analysis designed to assess equivalence or non-inferiority. Neither a margin nor such a method is reported in the registry record. The result should therefore be read as an unadjusted comparison of group means, not as proof that the schedules produce similar changes.

Secondary findings usually carry less weight than the prespecified primary result because they may be among several outcomes or analyses, and evaluating many comparisons can increase the chance of a nominally unusual result. Here, the registry lists one secondary outcome, but does not report a multiplicity strategy or a full analysis plan. The number of outcomes alone does not establish the full number of tests conducted. The record also lists no reported secondary analyses beyond the posted outcome information. Without a correction plan or prespecified hierarchy, the unadjusted secondary result is exploratory in interpretation.

The direction of the BPRS contrast cannot be translated confidently into “more improvement” or “less improvement” because the record does not state the change-score convention. The secondary result adds information about the posted data, but its reporting and analysis limitations mean it should not overrule or extend the primary finding.

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

• Change in Brief Psychiatric Rating Scale (BPRS) Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: patient acceptance is reported as a numeric scale score, and the registry gives a mean for each randomized group. A mean is the arithmetic average of the observed scores. It provides a compact description of the group but does not show the distribution of individual responses. In particular, the same average could arise from different patterns of ratings, and the registry record does not provide the score distribution.

The reported standard errors are 0.5 in each group. A standard error describes the precision of an estimated mean, rather than the spread of individual participants’ scores. It generally becomes smaller when an estimate is based on more information and when observations are less variable. It should not be mistaken for a standard deviation. The record reports the standard errors but does not provide the original statistical analysis method used to obtain the outcome results.

The group contrast is reported as a mean difference, defined in the posted comparison as the twice-daily group mean minus the once-daily group mean. For patient acceptance, the estimate is 2.2 units. A positive value therefore indicates a higher average score for twice-daily dosing on a scale where higher scores indicate less acceptance. The confidence interval from 0.814 to 3.586 describes a range of values compatible with the estimate under the method used to calculate it. The method and confidence level are not reported in the registry record, so additional assumptions about its construction should not be inferred.

The unadjusted p-value for this comparison is 0.002. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, under a statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The registry does not report the primary analysis model, the test used, or a prespecified significance threshold. Therefore, the reported p-value is best read as an unadjusted summary accompanying the posted contrast, not as a complete account of the trial’s planned statistical test.

The standardized effect estimate for the primary comparison is d = 1.112, and the pooled standard deviation is 1.978. In general, a standardized mean difference expresses the group contrast in standard-deviation units, which can make effects on different measurement scales easier to compare. It does not replace the scale-unit difference, which is more directly interpretable against the acceptance anchors. These standardized and pooled-spread estimates do not tell how participants’ ratings were distributed. Their derivation and role in the trial’s original analysis are not reported in the registry record.

The secondary BPRS result is also expressed as a difference in group means. Its estimated contrast is -8.36, with a confidence interval from -15.11 to -1.612. The negative sign reflects the stated subtraction order: the twice-daily mean minus the once-daily mean. The sign does not by itself determine which group had greater improvement, because the registry record does not state whether change was calculated as day-14 score minus baseline or baseline minus day-14 score. The listed standard errors are 2.64 for once-daily dosing and 2.21 for twice-daily dosing. The record does not give the underlying score distributions or the analysis model for this outcome.

Over-dispersion is a general concern when outcomes vary more than a statistical model assumes; in such cases, standard errors can be understated and uncertainty can appear too small. For continuous outcomes, the distribution and variability of scores can affect the suitability of a model. The posted summaries do not provide enough information to assess distributional assumptions or over-dispersion in this trial. This is a general methodological consideration, not a finding about the trial’s data.

Randomization helps balance measured and unmeasured characteristics on average across groups, but it cannot ensure identical groups in a small realized sample. The primary outcome counts were 12 and 18. The registry record does not describe stratification, covariate adjustment, allocation concealment, or the analysis population. It also does not report a prespecified method for missing outcomes, deviations from assigned dosing, or other protocol events. Those details matter when judging whether a simple comparison of posted means matches the intended randomized analysis.

Finally, interpretation depends on more than a p-value. The scale anchors, the estimated difference, its interval, the population represented, and the analysis plan all contribute. The record gives a difference and an interval, but does not report a threshold for a clinically meaningful acceptance difference or details of the analysis plan. A statistical contrast can therefore be described, while its importance beyond this sample remains uncertain.

11. Confidence Intervals and Precision

The confidence interval for the primary mean difference runs from 0.814 to 3.586 scale units, around an estimated difference of 2.2 units. With the contrast defined as twice-daily minus once-daily, the interval lies on the side of higher average acceptance scores for the twice-daily group. Since higher scores mean less acceptance on the stated scale, the interval is compatible with a less favorable mean rating for twice-daily dosing in this sample. The interval also shows that the exact size of the difference is uncertain; it does not identify one exact underlying contrast.

A confidence interval is a statistical way to express uncertainty around an estimate. In general, its interpretation depends on the method and assumptions used to calculate it. The confidence level and calculation method are not reported in the registry record, so the interval should not be assigned an unreported confidence level. Nor does an interval show the range of individual participants’ scores: it concerns uncertainty in the group contrast.

The endpoint counts are 12 for once-daily dosing and 18 for twice-daily dosing. These are modest group sizes, and the reported standard errors and interval should be considered alongside them. The registry does not report missing-data handling, an analysis population, or a prespecified meaningful-difference threshold. Consequently, precision in the statistical estimate does not settle how important the observed difference is in practice, or whether the estimate would be similar in another group of participants.

The BPRS contrast also has an interval, from -15.11 to -1.612, around an estimate of -8.36. Its interpretation is constrained by the unreported change-score convention and by its secondary status. Neither interval accounts for the broader uncertainty created by incomplete reporting about the analysis plan and outcome handling.

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 calculations are planning illustrations based on the observed effect, not a description of the trial’s original design assumptions. The figures are participants per arm, not total participants, because the outcomes are continuous; they are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set as a stated fraction of the observed effect. The registry record does not report the trial’s original sample-size justification or its original design assumptions.

The 80% power column describes the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions hold. The 90% power column uses a higher target chance of detecting the same specified effect. Power is a property of a planned study under assumed conditions; it is not a measure of the probability that the trial result is true.

The rows consider planning for 100%, 75%, and 50% of the observed effect. When the effect to detect is smaller, more participants are needed to distinguish it from random variation at the same power target and significance level. These figures are sensitive to the observed effect used as their starting point, so they should not be treated as a guaranteed design prescription or as evidence that the completed trial had adequate power. This is not observed power: it is a forward-looking planning illustration based on stated assumptions.

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 = 2.200; pooled standard deviation σ = 1.978.
2. n = 2 × (1.96 + 0.842)² × 1.978² / 2.200² = 12.7, rounded up to 13 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 <- 2.2                      # observed difference in means
sigma <- 1.97755259998673                     # 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(1549041)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 23 (80% power), 31 (90% power)
 50% of observed effect: n per arm = 51 (80% power), 68 (90% power)
power.t.test: 13.7 
Simulated power at n = 13 per arm: 0.778 (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. Multiplicity, Missing Data and Analysis Populations

The registry record identifies patient acceptance as the primary outcome and lists change in BPRS total score as a secondary outcome. It does not report a statistical analysis plan specifying how the primary and secondary outcomes were prioritized, whether further analyses were prespecified, or how multiplicity was handled. No adjustment for multiple comparisons is reported. The posted p-values are therefore unadjusted, and the registry does not provide enough detail to assess the full family of analyses that may have informed the results.

Multiplicity matters because the chance of observing at least one apparently unusual result can increase when many hypotheses are tested. In general, adjustment or a prespecified outcome hierarchy can help address that issue. Whether either approach was used in this trial is not reported in the registry record. The single listed secondary outcome does not establish that no other analyses were considered or conducted.

The registry record does not report how missing day-14 acceptance scores or missing BPRS measurements were handled. It does not describe an intention-to-treat population, a per-protocol population, or another analysis population. The outcome counts are reported by group, but there is no participant flow information explaining whether those counts include all randomized participants, or how any exclusions and withdrawals were treated.

Other details needed to evaluate the analysis, including the trial’s original sample-size justification, interim analyses, allocation procedures, covariate adjustment, and the statistical model, are not reported in the registry record. These omissions do not show that the methods were inadequate; they mean the posted record is insufficient to verify the planned approach or assess how departures from that approach might affect the estimates.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry record reports serious adverse events affecting 0 of 12 participants in the once-daily group and 0 of 18 in the twice-daily group. These are counts of participants affected, not a complete description of the types, timing, or duration of events. The record lists no serious adverse event terms. It also reports 0 participants affected by other adverse events in the once-daily group and 4 in the twice-daily group.

Counts should be read in the context of the group sizes and the information the record captures. The absence of reported serious adverse events in these groups does not establish that a regimen has no serious risks. A small trial and the absence of event-level details limit what can be concluded about uncommon events, comparisons between groups, or the range of possible adverse effects. Death counts are not reported in the registry record. The adverse-event figures do not establish a causal relationship between the assigned regimen and any event.

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

The posted primary result describes a difference in average day-14 acceptance ratings between the two dosing schedules. The once-daily group had a lower mean score on a scale where lower values are anchored to greater acceptability. The estimated contrast and its confidence interval indicate that the observed group means were separated in this sample, with the twice-daily group averaging a less favorable rating. This is a description of the posted outcome, not a complete account of the trial’s conduct or a guarantee that the same contrast would be observed in another sample.

The result does not establish why ratings differed. The record does not provide participant-level information, qualitative reasons for ratings, adherence data, or enough detail about missing observations to examine those possibilities. Nor does the day-14 endpoint establish how acceptance changed over time or whether the ratings reflected longer-term use.

The secondary BPRS result is distinct from the acceptance outcome. Its reported contrast should not be labeled as greater or lesser improvement without knowing the change-score convention. The registry summary’s hypothesis of similar psychopathology changes cannot be confirmed merely by comparing average values; a similarity claim needs a defined margin and appropriate analysis, neither of which is reported in the registry record.

More broadly, statistical evidence is not the same as evidence of clinical importance. The record does not report a threshold for a meaningful change in acceptance, and the interval gives uncertainty about the group contrast rather than the range of individual experiences. The small trial and incomplete reporting also limit the strength of broader conclusions. The findings do not establish that either schedule is suitable for a particular person, and they should not be used as individualized medical advice.

17. Why This Trial Matters Statistically

This trial poses a focused statistical question: whether patient acceptance differs between once-daily and twice-daily schedules when the comparison is randomized and conducted in parallel groups. Its primary endpoint is directly tied to the stated acceptance question, and the scale anchors make the direction of the average scores interpretable. Reporting both group means and a mean difference with an interval allows readers to consider the estimated contrast and its uncertainty rather than relying only on a p-value.

The study also illustrates why outcome hierarchy matters. Patient acceptance is primary, while BPRS change is secondary and addresses a separate clinical construct. The registry summary’s expectation of similar psychopathology changes cannot be established simply by observing two means; similarity requires a planned statistical framework. The distinction is important when interpreting secondary results, especially when multiplicity handling and analysis plans are not reported.

The record also shows how limited sample sizes affect precision and the scope of inference. The posted group counts are modest, and planning illustrations based on the observed effect change substantially when the assumed target effect is smaller. Such illustrations can help explain how sample size depends on the effect a study aims to detect, but they cannot stand in for the trial’s original design rationale.

Finally, this example highlights the value of complete registry reporting. Participant flow, missing-data methods, analysis populations, and the statistical plan are essential for assessing how estimates relate to the randomized design. The available results support a precise description of the posted averages and contrasts, while leaving important questions about analysis and generalizability unresolved.

18. Limitations

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

The registry record provides limited information for evaluating the trial beyond the posted group summaries. It does not report participant characteristics, detailed eligibility criteria, the allocation procedure, adherence, or participant flow. The primary outcome counts are 12 and 18, but the record does not explain the distribution of participants across the trial after randomization or whether any outcome observations were missing.

The primary endpoint is measured at day 14, so the posted result addresses acceptance at that time point only. The record does not report repeated acceptance measurements or longer-term follow-up. It also does not provide score distributions, which would help show whether the group averages reflect broadly similar participant responses or a more varied pattern.

The BPRS outcome is a change score from baseline to day 14, but the registry record does not state the subtraction convention. This prevents a firm interpretation of the sign of the group difference as more or less improvement. In addition, no equivalence or non-inferiority margin is reported for the hypothesis that psychopathology improvements would be similar across schedules.

The statistical analysis plan, analysis population, missing-data methods, and multiplicity approach are not reported in the registry record. The original sample-size justification and interim analyses are also not reported. The record lists no staff-acceptance result despite describing staff acceptance as an area of interest. Finally, the small group counts and the short listed endpoint timeframe constrain the scope of what these results can establish. These limitations reflect the information available in the record and do not by themselves show how the trial was conducted beyond what is documented.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Once-Daily Asenapine for Schizophrenia — NCT01549041.
• Registry record last updated 2014-05-26; status last verified 2013-11.
• Results first posted 2014-05-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed phase 4 randomized, unmasked, parallel-group trial sponsored by Duke University. It lists a planned enrollment of 30 and compares asenapine 10 mg in the evening with asenapine 5 mg twice daily. The primary outcome is patient acceptance at day 14, and the listed secondary outcome is change in BPRS total score from baseline to day 14.

The primary group summaries show lower average acceptance scores for once-daily dosing on the scale described in the record, with an unadjusted mean difference of 2.2 units. The secondary outcome is also posted, but its direction cannot be interpreted as more or less improvement without the change-score convention. Serious adverse-event counts are reported as zero in both groups; the registry also reports other adverse events in the twice-daily group. Important details about analysis methods, missing data, and participant flow are not reported in the registry record.