Efficacy, Safety, and Tolerability of Brexpiprazole (OPC-34712) as Maintenance Treatment in Adults With Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety, and Tolerability of Brexpiprazole (OPC-34712) as Maintenance Treatment in Adults With Schizophrenia (NCT01668797), a randomized phase 3 study. The primary outcome is Time From Randomization to Exacerbation of Psychotic Symptoms/Impending Relapse in Phase C..

2. Clinical Question

The endpoint was time-to-event rather than simply whether a participant met a relapse criterion by a particular visit. That distinction matters: a time-to-event outcome uses both whether an event occurred and when it occurred, while participants without a recorded event may contribute follow-up until their observation ends. The registry defines impending relapse using a set of clinical criteria, including worsening on the Clinical Global Impression of Improvement scale, specified Positive and Negative Syndrome Scale findings, hospitalization due to worsening illness, suicidal behavior or specified suicidal-ideation responses, and violent or aggressive behavior causing clinically significant injury.

The registry describes the study as evaluating brexpiprazole compared with placebo as maintenance treatment. The posted primary analysis reports a log-rank p-value of < 0.001 and arm-level hazard-ratio estimates with confidence intervals. These statistics address the time-to-event question, but the registry record does not provide a single directly stated treatment-versus-placebo hazard ratio with its confidence interval. The findings therefore need to be read with attention to what is reported and what remains unspecified, rather than treating every posted arm-level number as a direct between-group contrast.

3. Trial Design

This was a phase 3, randomized, quadruple-masked, parallel-group trial sponsored by Otsuka Pharmaceutical Development & Commercialization, Inc. The registry records an enrollment of 524 and a completed study. The listed start was 2012-10, and primary completion was 2015-01. The study compared brexpiprazole with placebo as maintenance treatment in adults with schizophrenia; each double-blind maintenance assignment was described as lasting 52 weeks.

The primary outcome was time from randomization to exacerbation of psychotic symptoms or impending relapse in Phase C, with follow-up described as up to 52 weeks. The primary analysis population was a full analysis set based on the ITT principle, but it had additional eligibility requirements: participants had to be randomized to double-blind treatment, take at least one dose of study medication in Phase C, and have at least one post-randomization efficacy evaluation in Phase C. The registry’s description of this population should be kept distinct from a claim that every randomized participant necessarily contributed to the primary analysis.

The registry also describes a single-blind stabilization phase, with 464 participants at risk in the adverse-event information. The double-blind maintenance safety groups list 97 participants for brexpiprazole and 104 for placebo. The primary efficacy arm records also list 96 participants for brexpiprazole and 104 for placebo. These are outcome-specific records and should not be treated as interchangeable denominators. The record does not explain the difference between the brexpiprazole efficacy and safety denominators.

The registry lists 29 outcome measures and 138 analyses. These counts indicate that the record contains multiple outcomes and analyses, but they do not establish which analyses were prespecified, how the study’s overall error rate was managed, or how missing observations were handled. Those details are not reported in the registry record. The study design can therefore be described from its recorded features, while unreported features of the protocol and analysis plan must remain unresolved.

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: Trial had Phase A (Conversion) (N= 406), Phase B (Oral Stabilization) (N= 464; 346 rolled over from Phase A and 118 entered directly into Phase B ) and Phase C (Double-Blind Maintenance) with (N= 202 rolled over from Phase B). Participants were randomized in to Phase C in a 1:1 ratio (brexpiprazole:placebo) to receive treatment for up to 52 weeks.

Phase A (Conversion Phase)

Reasons for not completing this period:

Phase B (Stabilization Phase)

Reasons for not completing this period:

Phase C (Double-Blind Maintenance Phase)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Based on the Intent-to-Treat (ITT) principle, the full analysis set of this trial was composed of all participants randomized to the double-blind treatment who took at least one dose of study medication in Phase C and who had at least one post-randomization efficacy evaluation in Phase C.

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: The enrolled sample was defined as all participants who signed the informed consent for the trial and entered Phase A or Phase B.

6. Primary Endpoint

The registry lists the primary outcome as Time From Randomization to Exacerbation of Psychotic Symptoms/Impending Relapse in Phase C., measured over From randomization to time of exacerbation of psychotic symptoms/impending relapse - up to 52 weeks.

The primary endpoint was the time from randomization to exacerbation of psychotic symptoms or impending relapse during Phase C, followed for up to 52 weeks. It is a time-to-event measure: the event is the first occurrence of a qualifying relapse criterion, and the time component distinguishes an earlier event from a later one. This approach is useful when the timing of deterioration matters and when participants may have different lengths of observed follow-up.

The registry’s definition includes several routes to meeting the endpoint. These include a Clinical Global Impression of Improvement score of >=5 combined with specified worsening on individual PANSS items or their combined score; a CGI-I score of 6 or 7; hospitalization due to worsening illness; suicidal behavior or a “yes” response to Questions 4 or 5 in the suicidal-ideation section of the C-SSRS; or violent or aggressive behavior resulting in clinically significant injury. The definition also refers to a >=20% increase in PANSS Total Score, and to hostility or uncooperativeness PANSS scores of >=5.

Combining several criteria can capture different forms of clinically meaningful worsening, but it also means the endpoint is not a single symptom score. A participant may meet the event definition through any one qualifying route. The primary outcome description calls the measure type a hazard ratio, while the reported comparison is a log-rank test. The registry record does not give further detail about the event-time model or censoring rules, so those analytical details should not be inferred from the endpoint label alone.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

What does a time-to-event analysis measure?

Time-to-event methods analyze both event occurrence and event timing. In this trial, the event was meeting any of the registry’s impending-relapse criteria, and the relevant time began at randomization. A participant who has not met a criterion by the end of observed follow-up is not equivalent to a participant who met one early; the timing information is central to the endpoint. In general, time-to-event analyses can also accommodate participants whose event status is not observed for the entire planned follow-up, by using their available information up to the point observation ends. The registry record does not describe the censoring rules used in this analysis, so the handling of particular follow-up patterns cannot be established from the posted results.

How should the log-rank result be read?

The log-rank test is a general method for comparing event-time distributions between groups. It evaluates whether the observed pattern of events over follow-up is compatible with the groups having the same underlying event-time experience, subject to its assumptions. It does not by itself provide a treatment effect size. The registry reports a log-rank p-value of < 0.001 for the primary comparison. That result is evidence against no difference in the event-time distributions under the test, but it does not say how large the difference is or establish the reason for it.

The record labels the primary measure as a hazard ratio and posts estimates and confidence intervals separately for the two arms. A hazard is an instantaneous event rate among participants who have not yet experienced the event. A hazard ratio compares hazards under a specified reference orientation; its interpretation depends on which group is in the numerator and denominator. Because the registry does not give a single treatment-versus-placebo estimate or explain the orientation of the arm-level values, the estimates should be reported as posted rather than converted into a contrast by assumption.

What does a confidence interval add?

In general, a confidence interval shows the uncertainty associated with an estimate under the statistical model and assumptions used to construct it. A narrower interval indicates greater precision on that scale, while a wider interval indicates that a broader set of values remains compatible with the data. An interval does not measure bias, prove that the model is correct, or account automatically for multiple testing. The primary arm-level intervals are 0.156 to 0.548 for the brexpiprazole estimate and 1.825 to 6.411 for the placebo estimate. Their width matters when judging the precision of those estimates, but they are not a confidence interval for a directly reported treatment contrast.

What is the binary secondary comparison?

The secondary outcome is the percentage of participants meeting exacerbation of psychotic symptoms or impending-relapse criteria in the double-blind maintenance phase, assessed at baseline and Week 52/Early Termination. The posted values are 13.54% for brexpiprazole and 38.46% for placebo. A binary analysis treats each participant’s recorded outcome as meeting or not meeting the criteria over the defined assessment period. It does not use the exact timing of an event in the same way as the primary time-to-event analysis.

The recalculated risk difference is -0.249, with a 95% confidence interval from -0.365 to -0.133. A risk difference expresses the difference between the two recorded proportions on an absolute scale; the negative sign reflects the order used for the recalculation, brexpiprazole relative to placebo. The recalculated risk ratio is 0.352, with an interval from 0.201 to 0.617, and the recalculated odds ratio is 0.251, with an interval from 0.124 to 0.507. Risk ratios compare proportions directly, whereas odds ratios compare odds. When the outcome is not rare, those scales can differ meaningfully, so they should not be described as if they were the same quantity.

The recalculated p-value for the binary comparison is <0.001. It is an unadjusted calculation from the posted summary statistics. The registry’s own analysis uses a chi-squared test and reports p < 0.001. Different analysis specifications or precision can yield different reported p-value thresholds; the posted record does not explain the difference. Since no discrepancy flag is recorded, the recalculation is supplemental and does not replace the sponsor’s analysis.

What do the planning illustrations mean?

The registry-based planning illustration uses the observed secondary effect as a reference and considers detecting 100% of that observed effect, 75% of the observed effect, or 50% of the observed effect. For the full observed effect, the illustration gives 48 participants per arm for 80% power and 64 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 92 participants per arm for 80% power and 123 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 220 participants per arm for 80% power and 294 participants per arm for 90% power.

These are planning illustrations, not observed power and not evidence that the original trial was designed using those assumptions. The stated calculation assumptions are a two-sided significance level of 0.05, equal allocation, a normal approximation, and an effect defined as the stated fraction of the observed effect. The registry record does not report the trial’s own sample-size justification. In general, sample-size planning depends on assumptions about the target effect, variability or event frequency, significance level, power, allocation, and analysis method. A planning estimate cannot establish that a trial was adequately powered for every endpoint or subgroup.

Why can over-dispersion matter?

General statistical note: over-dispersion arises when observed variability exceeds what a statistical model assumes. If a model underestimates variability, standard errors may be too small and confidence intervals too narrow, potentially making p-values appear more compelling than warranted. This concept is relevant to count outcomes, but the primary endpoint is described as time-to-event and the secondary measure is binary. The registry record does not report an over-dispersion assessment or identify a count-model analysis for these results; this general issue should not be mistaken for a documented problem in this trial.

10. Analyses Reported by the Sponsor

The sponsor’s primary analysis reports a log-rank test with p < 0.001. For the secondary binary outcome, the sponsor’s reported analysis is a chi-squared test with p < 0.001. Those are the registry’s own analyses and remain the principal reported inferential results. The posted recalculation for the secondary outcome is an unadjusted analysis of summary statistics: it gives a risk difference of -0.249, a 95% confidence interval from -0.365 to -0.133, and p <0.001.

The recalculated p-value and the sponsor’s p-value are both reported as threshold values, not exact values, and their thresholds are not identical. The record does not explain the difference, and the recalculation does not reproduce the sponsor’s specified analysis. It is best understood as a complementary check using a simple unadjusted comparison, not as a correction to or replacement for the registry analysis. No discrepancy is flagged in the record.

For the primary endpoint, the registry’s reported log-rank result is available, but no two-arm recalculated effect estimate is posted. The primary outcome is a time-to-event endpoint, and the record’s arm-level hazard-ratio values do not supply a directly reported treatment-versus-placebo contrast. The sponsor’s analysis is therefore the appropriate source for the primary inferential result, while the limits of the posted effect-size reporting should remain explicit.

11. Multiplicity, Missing Data and Analysis Populations

The record contains many outcome and analysis entries: 29 outcome measures and 138 analyses. A larger set of tests raises a general multiplicity concern because repeated testing can increase the chance of at least one apparently notable result under a global null situation. That concern does not establish that a reported result is false; it affects how much confirmatory weight should be placed on isolated findings. The registry record does not report a multiplicity adjustment, a testing hierarchy, or which outcomes and analyses were designated as primary before the results were known.

The primary outcome is identified as time from randomization to exacerbation or impending relapse in Phase C, and the sponsor reports a log-rank p-value of < 0.001. The secondary endpoint has a sponsor-reported chi-squared p-value of < 0.001 and an unadjusted recalculated p-value of <0.001. These p-values are not evidence that all recorded analyses were controlled for multiplicity. The record also does not report interim analyses, stopping rules, or whether any alpha-spending approach was used; none should be assumed.

The analysis population is described as based on the ITT principle but is restricted to participants randomized to double-blind treatment who took at least one dose in Phase C and had at least one post-randomization efficacy evaluation in Phase C. This definition is important because it specifies who qualified for the full analysis set. It does not establish how participants with missing measurements were handled, how incomplete follow-up affected event-time analysis, or whether any imputation or sensitivity analyses were conducted. Those details are not reported in the registry record.

Missing data can affect estimates when the likelihood or timing of missing observations is related to outcome status or treatment assignment. General statistical practice may include defining censoring, using appropriate assumptions for incomplete outcomes, and testing sensitivity to those assumptions. The registry record does not provide enough information to assess these procedures. The count of participants in an outcome analysis also differs from the total enrollment and from safety denominators, and the record does not explain every denominator difference. Interpretation should therefore stay anchored to the stated population for each result rather than presuming that all enrolled participants contributed identically to every analysis.

12. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: schizophrenia (4.8%), psychotic disorder (3.8%), hepatic enzyme increased (1.0%), angina unstable (1.0%), arrhythmia (1.0%).

The adverse-event record gives serious adverse events for 34 of 464 participants in the single-blind stabilization phase, 3 of 97 in the brexpiprazole double-blind maintenance phase, and 11 of 104 in the placebo double-blind maintenance phase. It also gives other adverse events for 148 of 464 participants in stabilization and 0 of 97 and 0 of 104 in the respective maintenance groups. These are the posted counts and denominators; no new percentages are calculated from them.

The stabilization phase and double-blind maintenance groups are different periods and populations, so their figures should not be treated as a direct randomized comparison. Even between the maintenance groups, event counts alone do not describe event timing, duration, severity beyond the serious-event classification, or differences in observation and reporting. The registry lists serious-event terms with percentages, including Schizophrenia at 4.8%, Psychotic disorder at 3.8%, and Hepatic enzyme increased, Angina unstable, Arrhythmia, and Suicidal ideation each at 1.0%. The record does not clarify in this summary how those term percentages relate to each phase or denominator.

Death counts are not reported in the registry record. These adverse-event figures describe what was recorded; by themselves they do not establish causation or provide a complete comparative safety assessment.

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

The primary result indicates that the registry’s log-rank analysis found strong evidence of a difference between the brexpiprazole and placebo event-time distributions for the defined impending-relapse endpoint: p < 0.001. The arm-level estimates and intervals provide additional posted information, but the registry does not state a single treatment-versus-placebo hazard ratio with a confidence interval. The result is therefore most clearly described as a statistically notable primary time-to-event comparison, with limitations in how the comparative effect size is presented.

The secondary binary outcome points in the same direction, with a lower recorded proportion meeting the criteria in the brexpiprazole group than the placebo group. Its recalculated risk difference and confidence interval describe an unadjusted contrast based on the posted summary data. The sponsor’s chi-squared result and the recalculation are related analyses but not identical procedures, and the recalculation does not replace the sponsor’s result.

Neither a low p-value nor a confidence interval settles every question about the result. P-values do not show the probability that a treatment effect is real, and confidence intervals do not address unmeasured bias or every uncertainty in endpoint definition, missingness, or analysis choice. The registry does not report the detailed missing-data procedures, multiplicity strategy, or trial-specific sample-size justification. Those gaps limit assessment of the full inferential context.

The findings also do not establish that every participant would experience the same outcome, that the result applies to people outside the study population, or that the posted safety counts capture every relevant consequence. The registry describes adults with schizophrenia and a 52-week maintenance comparison; it does not provide a basis for extending these results beyond that context. Statistical interpretation should remain descriptive of the recorded groups, endpoints, follow-up, and analyses, without turning the observed group pattern into individualized advice.

14. Why This Trial Matters Statistically

This trial illustrates why endpoint type matters in clinical research. The primary outcome is time to impending relapse, not merely a final-visit status. Time-to-event methods use the timing of events and can incorporate available follow-up when event status is not observed throughout the full period, although the registry does not report its censoring rules. The secondary outcome reduces the relapse question to a binary measure over a specified assessment period. These analyses can complement one another while answering distinct questions.

It also shows why a p-value should not be read in isolation. The primary log-rank result is reported as p < 0.001, while the registry posts arm-level hazard-ratio estimates rather than one direct comparative estimate and interval. A statistically strong test result can coexist with incomplete reporting of an interpretable effect-size contrast. Effect estimates and their uncertainty are essential for understanding magnitude and precision, not only whether a test crosses a threshold.

The secondary outcome provides a practical contrast on several scales: risk difference, risk ratio, and odds ratio. These measures answer different questions and can communicate an absolute or relative comparison. The recalculation is explicitly unadjusted, while the sponsor’s own chi-squared test remains the registry’s reported analysis. Keeping those roles distinct helps prevent a simple recalculation from being mistaken for a full protocol-based analysis.

Finally, the registry lists many outcomes and analyses but does not report the multiplicity strategy, missing-data procedures, interim analyses, or sample-size justification. Those omissions make it important to distinguish confirmatory evidence from supportive or exploratory results. Transparent reporting of the analysis population, estimand, handling of incomplete follow-up, effect estimates, and multiplicity decisions is central to evaluating how precisely the results answer the original clinical question.

15. Limitations

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

Several limitations arise from the information recorded for this specific study. First, the primary outcome description labels the measure as a hazard ratio, but the posted values are presented by arm and do not include one explicit treatment-versus-placebo hazard ratio with its confidence interval. The log-rank p-value supports a comparison of event-time distributions, but the comparative effect size is less straightforward to interpret from the registry’s displayed estimates alone.

Second, the primary endpoint combines multiple routes to impending relapse, including symptom-scale thresholds, hospitalization, suicidal behavior or specified suicidal-ideation responses, and violent or aggressive behavior causing clinically significant injury. Such a composite can capture a broad range of deterioration, but the registry record does not provide the contribution of each criterion to the overall result. It is not possible from the posted summary to determine which components primarily drove the event pattern.

Third, the efficacy and safety records use different denominators. The primary efficacy groups list 96 participants for brexpiprazole and 104 for placebo, while the maintenance safety groups list 97 and 104. The record does not explain the efficacy denominator difference. The full analysis set also requires at least one dose and one post-randomization efficacy evaluation, so the population is not simply all 524 enrolled participants.

Finally, the registry does not report detailed missing-data handling, censoring rules, multiplicity procedures, interim analyses, or the trial’s own sample-size justification. The secondary recalculation is unadjusted and should not be viewed as a substitute for the sponsor’s analysis. Safety counts are descriptive, and death counts are not reported in the registry record. These reporting limits constrain the precision of conclusions that can be drawn from the registry summary alone.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Efficacy, Safety, and Tolerability of Brexpiprazole (OPC-34712) as Maintenance Treatment in Adults With Schizophrenia — NCT01668797.
• Registry record last updated 2017-01-13; status last verified 2016-11.
• Results first posted 2017-01-13.
• 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.

19. Record Summary

The registry describes a completed phase 3, randomized, quadruple-masked, parallel-group study of brexpiprazole versus placebo as maintenance treatment in adults with schizophrenia. Enrollment was 524; the listed study start was 2012-10 and primary completion was 2015-01. The double-blind maintenance assignments were described as lasting 52 weeks.

The primary endpoint was time from randomization to exacerbation of psychotic symptoms or impending relapse in Phase C. The sponsor’s log-rank analysis reported p < 0.001. The registry also posts arm-level hazard-ratio estimates and confidence intervals, but not one direct treatment-versus-placebo estimate and interval. The secondary relapse measure was directionally consistent with the primary finding; its sponsor analysis used a chi-squared test, and an unadjusted recalculation gives a risk difference of -0.249 with a 95% confidence interval from -0.365 to -0.133.

The registry does not report several details needed for fuller evaluation, including multiplicity procedures, missing-data handling, and the study’s sample-size justification. Safety records list serious adverse-event counts by phase and group; death counts are not reported in the registry record.