A Study to Test if TV-46000 is Safe for Maintenance Treatment of Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Test if TV-46000 is Safe for Maintenance Treatment of Schizophrenia (NCT03893825), a randomized phase 3 study. The primary outcome is Number of Participants With Adverse Events (AEs).

2. Clinical Question

The study’s primary objective was long-term safety and tolerability. Adverse events were defined without regard to whether they were considered causally related to study drug, so the endpoint is a broad account of medical occurrences during the stated timeframe. Serious adverse events were separately defined using outcomes such as death, life-threatening events, hospitalization, persistent or significant disability, congenital anomaly or birth defect, and other important events requiring intervention to prevent one of those outcomes.

The posted comparison is useful for describing the observed counts across the two schedules. However, the record does not report a detailed statistical analysis plan, an adjusted estimate, or a protocol-based interpretation of this outcome. The numerical comparison should therefore be read alongside its uncertainty and the limitations of the registry-level information.

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group study. The registry lists an enrollment of 336 and the condition as schizophrenia. It is marked completed. The study title and description identify TV-46000 as a risperidone extended-release injectable suspension for subcutaneous use as maintenance treatment in adult and adolescent participants.

Two active-drug schedules are shown. In the q1m group, TV-46000 was administered at baseline and every 4 weeks thereafter for up to 56 weeks. In the q2m group, TV-46000 was administered at baseline and every 8 weeks thereafter, with placebo injections 4 weeks after baseline and every 8 weeks thereafter. The registry says all participants received active drug. The posted safety groups contain 172 participants in the q1m arm and 162 in the q2m arm.

The registry describes different planned participation periods for new and rollover participants. For new participants, participation was planned to last up to 80 weeks, including screening, oral conversion and stabilization, a double-blind maintenance stage, and follow-up. For rollover participants, participation was planned to last up to 64 weeks, including the maintenance stage and follow-up. Participants who left the study early were to have follow-up procedures and assessments, and treatment during follow-up was left to the investigator’s judgment.

The primary outcome timeframe is stated as baseline up to Week 64. That timeframe should not be treated as identical to the maximum planned participation period for every participant. The registry does not report further detail about the randomization procedure, allocation concealment, masking implementation, or the original design assumptions for the statistical analysis. The two arm descriptions are also truncated after the maximum-dose information, so additional dosing details are not available in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants who were treated with TV-46000 once monthly (q1m) or once every 2 months (q2m) during Study TV46000-CNS-30072, continued their assigned treatment. Participants who were treated with placebo during Study TV46000-CNS-30072 were randomized in 1:1 to receive TV-46000 q1m or q2m subcutaneous (SC) injections at equivalent to oral dose on which they were stabilized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The safety analysis set included all participants who received at least 1 dose of TV46000 in TV-46000-CNS-30072 study or in TV46000-CNS-30078 study.

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 intent-to-treat (ITT) analysis set included all randomized participants who were randomized either in Study TV46000-CNS-30072 for roll-over participants or in Study TV46000-CNS-30078.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Adverse Events (AEs), measured over Baseline up to Week 64.

The primary endpoint is the number of participants with adverse events, measured from baseline up to Week 64. It is a participant-level count: a participant is counted if an adverse event is recorded, rather than the result representing the total number of separate event episodes. The posted results show 64 participants with adverse events among 172 in the q1m group and 74 among 162 in the q2m group.

The registry defines an adverse event as any untoward medical occurrence in someone who received study drug, whether or not a causal relationship to treatment was considered possible. This broad definition is useful in a safety assessment because it captures medical occurrences during treatment without limiting the tally to events judged treatment-related. It does not, on its own, distinguish expected from unexpected events or determine whether treatment caused an event.

Serious adverse events form a clinically important subset, with the record defining seriousness by outcomes or circumstances such as death, a life-threatening event, inpatient hospitalization, or significant disability. The main endpoint combines the broader adverse-event concept and therefore should not be interpreted as a count of serious events alone. The registry directs readers to its reported adverse-event section for summaries of serious and other non-serious events.

The endpoint is appropriate to the study’s stated primary objective of assessing long-term safety and tolerability. A participant-level count is straightforward to describe, but it does not capture event timing, recurrence, duration, or severity in a single summary. Those details require separate event listings or analyses, and the registry does not provide them within this primary endpoint summary.

7. Results Posted in the Registry

• TV-46000 q2m: 45.7% (74/162) versus 37.2% (64/172) on control; risk difference 8.5 percentage points (95% CI -2.1 to 19.0), risk ratio 1.23 (0.95–1.59); unadjusted two-proportion z-test p = 0.116.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either had at least one adverse event recorded within the outcome timeframe or did not. The posted counts are 64 of 172 for q1m and 74 of 162 for q2m. A binary outcome can be summarized as a count and as a proportion, and a comparison can be presented as a difference between proportions, a ratio of risks, or an odds ratio. These measures use the same underlying event information but express the contrast on different scales.

What does the risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the other group. Here, the comparison is oriented as q2m relative to q1m. A positive estimate points toward a higher observed event proportion in q2m, while a negative estimate would point toward a lower observed event proportion in q2m. A value of zero represents no difference in the proportions. The posted interval crosses zero, so it includes both directions as well as no difference.

A risk difference is often easy to interpret in absolute terms, but its precision depends on the observed counts and group sizes. The point estimate is only one estimate from the study data. Its confidence interval communicates a range of values reasonably compatible with the data under the calculation’s assumptions; it is not a guarantee that the true value lies within that particular interval.

How should the p-value be read?

The reported unadjusted p-value is 0.116. In general, a p-value describes how unusual data at least this discrepant from a specified null model would be if that model were true, under the method’s assumptions. It is not the probability that the null hypothesis is true, the probability that chance alone produced the result, or a measure of clinical importance. The posted record does not give a protocol-defined testing plan for this comparison, so the p-value should be read as an unadjusted summary rather than proof of a prespecified confirmatory test.

The p-value and confidence interval are related summaries of uncertainty, but neither provides a full account of the data. The interval is particularly useful because it shows that the estimate is not tightly resolved around one direction. The p-value should not be used by itself to claim equivalence, safety similarity, or a clinically important difference.

Why distinguish an unadjusted recalculation?

The displayed comparison is a simple unadjusted recalculation from the posted group counts. It does not account for any covariates, stratification factors, repeated observations, or other adjustments. The registry record does not describe whether the sponsor used a different model for its own analysis or how such an analysis might relate to the displayed comparison. Because no discrepancy is flagged for this result, the posted comparison can be described as shown, while still recognizing that the full analysis details are not available in the record.

Unadjusted comparisons can be transparent and reproducible from summary counts, but randomization does not make every feature of the observed groups identical. Adjusted approaches may be planned to improve precision or account for design factors. Whether an adjustment is suitable depends on the study design and the prespecified analysis. Those details are not reported in the registry record, so no adjusted result should be inferred.

What does the endpoint leave out?

Counting participants with any adverse event gives each participant a binary status for this endpoint, regardless of whether they had one event or multiple events. It also does not distinguish the seriousness or duration of an event in the primary count. Separate serious and non-serious event summaries can add information, but they do not change the meaning of the main endpoint. As a general statistical point, summaries that collapse event frequency and severity can conceal differences in the kinds of events experienced.

Exposure and observation time can also matter when interpreting safety counts. The endpoint timeframe is baseline up to Week 64, while the planned total participation period differs between new and rollover participants and may include follow-up. The record does not describe how time at risk, early withdrawal, or incomplete observation was handled in the primary comparison. It is therefore not possible to infer a person-time analysis or to assume that every participant contributed the same amount of observed time.

Why can over-dispersion matter in other outcomes?

As a general statistical concept, count outcomes can show over-dispersion when their variability exceeds what a simple count model expects. In that setting, a model that assumes less variability than the data contain can produce overly narrow uncertainty intervals. The current primary endpoint is a participant-level binary outcome, not a count of event episodes, and the registry does not report an over-dispersion assessment or a count model for it. This concept is relevant when interpreting analyses of repeated event totals, but it should not be attributed to this study’s posted primary comparison.

10. Confidence Intervals and Precision

The comparison’s precision is best understood from the confidence interval, not from the point estimate alone. For the q2m-versus-q1m risk difference, the posted interval crosses zero. That means the results are compatible with a lower event proportion in q2m, no difference, or a higher event proportion in q2m, under the calculation used. The interval’s span indicates that the direction and magnitude of the difference are not pinned down narrowly by these data.

A confidence interval is a statistical procedure: under its assumptions, intervals constructed in this way would contain the underlying parameter at the stated coverage rate in the long run. It is not a probability statement about this one realized interval or a guarantee about the true value. The registry does not specify a confidence level in the displayed comparison, so a level should not be inferred from the record.

The p-value for the unadjusted comparison is 0.116. This should be read together with the interval rather than as a stand-alone decision. The interval’s inclusion of zero makes clear that the observed contrast does not distinguish a difference from no difference with high precision under this calculation. It also does not demonstrate that the schedules are equivalent; showing equivalence would require a prespecified margin and a suitable analysis, neither of which is reported in the registry record.

Precision is influenced by the number of participants and events, as well as the analysis method and outcome variability. Here, the group sizes are 172 and 162, and the observed event counts are 64 and 74. Those counts are informative for this comparison, but the record does not report a sample-size justification for the original trial or a target precision for this safety endpoint. The planning illustrations elsewhere on the page use the observed effect for hypothetical designs and should not be mistaken for a description of the actual trial’s precision target.

11. 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 table and its curve are planning illustrations based on the observed effect, not a reconstruction of the trial’s original design. For this binary outcome, figures are participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size assumptions or justification.

The table shows planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For 100% of the observed effect, the illustration gives 530 participants per arm for 80% power and 709 participants per arm for 90% power. For 75% of the observed effect, it gives 936 participants per arm for 80% power and 1,252 participants per arm for 90% power. For 50% of the observed effect, it gives 2,088 participants per arm for 80% power and 2,794 participants per arm for 90% power.

In plain language, the 80% power column represents the planned number per arm under these assumptions for a design with an 80% chance of detecting the specified effect if that effect is real. The 90% column describes the larger planned number per arm for a design targeting a 90% chance under the same assumptions. Smaller effects are harder to distinguish from random variation, so planning for smaller fractions of the observed effect requires more participants per arm. The curve gives a visual version of this relationship; it is a planning aid, not an additional result from the trial. This is not observed power.

12. 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.372; treatment proportion p₁ = 0.457; average p̄ = 0.414.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6967 = 1.3655.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6941 = 0.5842.
4. n = (1.3655 + 0.5842)² / (0.0847)² = 529.9, rounded up to 530 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
p0 <- 0.372093023255814                          # control proportion
p1 <- 0.45679012345679                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3893825)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 530 (80% power), 709 (90% power)
 75% of observed effect: n per arm = 936 (80% power), 1,252 (90% power)
 50% of observed effect: n per arm = 2,088 (80% power), 2,794 (90% power)
power.prop.test: 529.9 
Simulated power at n = 530 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a detailed statistical analysis plan for the primary safety comparison. It does not state whether this comparison was part of a prespecified hypothesis-testing sequence, whether any covariate adjustments were planned, or how the displayed result relates to a sponsor analysis. The posted unadjusted p-value should therefore not be assumed to reflect a complete confirmatory testing strategy.

Multiplicity arises when several outcomes, comparisons, timepoints, or subgroups are tested. If many tests are interpreted together without an adjustment or an ordering strategy, the chance of at least one apparently notable result can increase. The record lists three outcome measures but no secondary results, and it does not report a multiplicity-control method. Whether multiplicity adjustments were used elsewhere is not reported in the registry record.

How missing outcomes and incomplete follow-up were handled is also not reported in the registry record. The study description says participants who withdrew before completing the maintenance stage would have follow-up procedures and assessments, but it does not specify the analysis treatment of missing endpoint data, early discontinuation, or participants without an assessment. The endpoint timeframe extends to Week 64, while planned participation length varies by participant type. The record does not say whether the primary comparison used all available observations, an imputation method, or another approach.

The safety analysis population is defined as participants who received at least 1 dose of TV-46000 in either of two named studies. The registry record does not give a complete participant-flow account for this outcome or explain how that population relates to the overall enrollment entry. The posted group totals should therefore be interpreted as the analysis groups shown, not as evidence that every enrolled participant had complete outcome data.

These omissions limit assessment of robustness. They do not imply that a particular method was or was not used; the statistical plan, missing-data rules, and multiplicity approach are simply not reported in the registry record.

14. 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: schizophrenia (1.2%), anaemia (0.6%), acute myocardial infarction (0.6%), angina pectoris (0.6%), hyperglycaemia (0.6%).

The serious adverse event summary reports 8 participants at risk and affected in the q1m group and 11 in the q2m group. The other, non-serious adverse event summary reports 10 participants affected in the q1m group and 12 in the q2m group. The record also lists 2 deaths for q1m and 1 for q2m. These are separate reported safety figures and should not be added to, or substituted for, the primary count of participants with any adverse event.

The registry lists serious adverse event terms including schizophrenia at 1.2%, and anaemia, acute myocardial infarction, angina pectoris, hyperglycaemia, and depression at 0.6% each. Those terms are a summary of reported serious events; the record excerpt does not give individual event narratives, timing, recurrence, or a causal assessment for each term. The primary adverse-event definition includes events regardless of possible causal relationship to study drug.

These figures are descriptive. The record does not provide a comparative statistical analysis of serious events, nor does it establish that any listed event was caused by treatment. Small event counts can also yield imprecise comparisons, and the registry summary is not a substitute for detailed safety listings or clinical review.

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

The posted data describe adverse events in two groups assigned to different TV-46000 maintenance schedules. The primary outcome counts participants with at least one adverse event over baseline up to Week 64. The simple unadjusted comparison points toward a higher observed event proportion in q2m, but its confidence interval crosses zero and its unadjusted p-value is 0.116. The data do not precisely resolve whether the schedules differ on this broad outcome.

This finding does not establish equivalence or non-equivalence. A lack of a clear separation in an unadjusted comparison is not proof that the schedules have the same safety profile. Conversely, the positive point estimate alone is not proof that the q2m schedule causes more adverse events. The confidence interval reflects uncertainty in the estimated difference, and the registry does not report an equivalence margin or a detailed confirmatory analysis plan.

The outcome also has limits as a summary of safety. It counts participants with any adverse event and does not, by itself, characterize how many events each participant experienced, how long events lasted, how severe they were, or whether they were judged related to treatment. Serious adverse event counts and the listed terms add descriptive context, but the available summary does not provide enough information to infer causation or compare the clinical importance of event profiles.

Because both groups received active TV-46000, the comparison speaks to the two schedules as represented in the registry, not to treatment versus no treatment. The q2m arm also included placebo injections as part of its schedule. No conclusion about the effect of TV-46000 versus placebo alone follows from this comparison.

Finally, these posted results should be viewed as registry-level evidence. Details on missing data, follow-up completeness, multiplicity, and the full analysis plan are not reported in the registry record. Those gaps matter when judging how completely the reported comparison captures the study’s intended safety question.

16. Why This Trial Matters Statistically

This trial illustrates why the description of a clinical endpoint matters as much as the numerical comparison. The primary measure is the number of participants with any adverse event, a broad participant-level outcome aligned with the study’s stated safety and tolerability objective. It is distinct from the number of event episodes, serious events alone, or an assessment of whether an event was caused by study drug.

It also shows how uncertainty should shape interpretation. The q2m-versus-q1m point estimate is positive, but the confidence interval crosses zero and the unadjusted p-value is 0.116. Reporting the estimate alongside its interval avoids treating one observed difference as a settled conclusion. It also avoids interpreting a non-definitive comparison as evidence of equivalence.

The trial’s design adds context: it was randomized and parallel-group, and the two groups followed different active-drug schedules. This makes the comparison relevant to the schedules studied, while limiting what can be said about active treatment versus no active treatment. The registry’s statement that all participants received active drug is important for defining the contrast accurately.

Finally, the record highlights the distinction between a trial’s own design and a hypothetical planning exercise. The sample-size illustrations apply stated assumptions to fractions of the observed effect; they do not tell us why the actual study enrolled its participants or whether it was designed around this particular safety comparison. Keeping these separate prevents a planning calculation from being mistaken for evidence about the trial’s original statistical intent.

17. 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 leaves important details unavailable for interpreting the comparison. The original sample-size justification, the statistical analysis plan, randomization procedure, allocation concealment, and implementation of masking are not reported in the registry record. The planning table is a separate illustration and cannot fill in those protocol details.

The handling of missing data, early withdrawal, differing follow-up, and incomplete observation is not reported. This matters because the outcome timeframe is baseline up to Week 64, while the planned total participation period differs between new and rollover participants. The record describes follow-up procedures for early withdrawals but does not specify how such participants were included in the primary endpoint analysis.

The analysis population is defined by receipt of at least 1 dose of TV-46000 in either of two named studies. The registry does not explain how this set maps to the overall enrollment entry or provide a full participant-flow summary for the outcome. The posted counts should be understood within the displayed safety groups rather than assumed to cover every enrolled participant.

The endpoint is broad and does not distinguish event frequency, duration, severity, or causality in its primary count. Serious and other non-serious event summaries provide additional descriptive information, but the registry excerpt does not include detailed narratives or a statistical comparison for those categories. In addition, the arm descriptions are truncated, limiting what can be said about dose details beyond the schedules explicitly described.

Finally, no secondary outcome results are posted here, and multiplicity procedures are not reported. These limitations restrict the strength and scope of conclusions that can be drawn from this registry-level safety comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study to Test if TV-46000 is Safe for Maintenance Treatment of Schizophrenia — NCT03893825.
• Registry record last updated 2022-12-07; status last verified 2022-12.
• Results first posted 2022-10-04.
• 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.

21. Record Summary

The registry record describes a completed Phase 3, randomized, quadruple-masked, parallel-group study of TV-46000 as maintenance treatment for adults and adolescents with schizophrenia. Enrollment is listed as 336. The primary objective was long-term safety and tolerability, with the primary endpoint defined as participants with adverse events from baseline up to Week 64.

The posted comparison is between q1m and q2m TV-46000 schedules. Counts with adverse events were 64 of 172 in q1m and 74 of 162 in q2m. The unadjusted comparison has a positive risk-difference estimate for q2m relative to q1m, an interval crossing zero, and a p-value of 0.116. Serious adverse events, other non-serious events, and deaths are also summarized descriptively.

The registry does not report the original sample-size assumptions, detailed analysis plan, missing-data methods, or multiplicity strategy. The displayed sample-size values are planning illustrations under stated assumptions, not the trial’s original design rationale.