Study of Paliperidone Palmitate 3 Month and 1 Month Formulations for the Treatment of Patients With Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Paliperidone Palmitate 3 Month and 1 Month Formulations for the Treatment of Patients With Schizophrenia (NCT01515423), a randomized phase 3 study. The primary outcome is Percentage of Participants Without Relapse at Week 48 During the Double-Blind Phase.

2. Clinical Question

The endpoint is clinically framed as remaining free of a defined relapse event, rather than as a change in a symptom score alone. Its interpretation depends on the event definition, the analysis population, the length of follow-up, and the uncertainty around the comparison. The posted results describe a randomized parallel-group comparison during the double-blind phase; they do not by themselves answer how outcomes would compare in populations or settings beyond this trial.

3. Trial Design

This was a phase 3, randomized, multicenter, double-blind, parallel-group study. The registry record describes the study as a non-inferiority comparison of paliperidone palmitate 3-month and 1-month formulations for participants with schizophrenia. The study's stated purpose was to assess whether the 3-month formulation was as effective as the 1-month formulation in participants stabilized on the 1-month formulation. The record lists enrollment of 1429 and a completed status.

The trial began in 2012-05, and primary completion was in 2015-02. During the double-blind phase, the two primary endpoint groups were the 3-month formulation and the 1-month formulation. Their primary endpoint analysis populations were 458 and 490, respectively. These endpoint populations are not the same description as overall trial enrollment: the primary analysis set required random assignment during the double-blind phase, at least one study-drug dose, and no errors in delivery of active treatment. The registry record does not report further reasons for the difference between the overall enrollment and these endpoint analysis counts.

The intervention list includes several dose strengths for each formulation and a placebo described as 20% Intralipid. The arm descriptions identify the 3-month and 1-month injection intervals. The brief summary says participants were stabilized on the 1-month formulation before the comparison. The details of stabilization, treatment switching, dose selection, and the sequence of study periods are not reported in the registry record, so the posted description should not be expanded into assumptions about those procedures.

The official title identifies a double-blind non-inferiority design, but the non-inferiority margin, the planned statistical model, the hypothesis-testing procedure, and the original design assumptions are not reported in the registry record. The record also does not list formal analysis results for the primary outcome. Accordingly, the arm-level percentages and the unadjusted recalculated comparison describe the posted data, but they do not replace a prespecified sponsor analysis of non-inferiority.

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: 1429 participants received at least 1 dose of the study agent in the Open-label Phase, out of which 1016 participants were randomized into the Double blind Phase (Safety population).

Open Label Phase

Reasons for not completing this period:

DOUBLE BLIND

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (mITT) analysis set included all participants who were randomly assigned to treatment during Double-blind Phase, received at least 1 dose of study drug and did not have any errors in delivery of active treatment. Here,N=number of participants analysed is the total participants who were 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: The safety analysis set included all participants who were randomly assigned to treatment during the Double-blind Phase and received at least 1 dose study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Without Relapse at Week 48 During the Double-Blind Phase, measured over Up to 48 weeks.

The primary endpoint is the percentage of participants without relapse at Week 48 during the double-blind phase, with a timeframe of up to 48 weeks. A participant is counted as without relapse if no event meeting the registry's relapse definition occurs during the relevant follow-up. The measure is binary at the participant level: each participant either meets the no-relapse definition or does not. The reported percentage then describes the share of the analysed group classified as remaining without relapse.

The relapse definition combines clinically consequential events and symptom-based criteria. It includes psychiatric hospitalization; specified increases in total Positive and Negative Syndrome Scale (PANSS) score from randomization; deliberate self-injury or violent behavior resulting in suicide or clinically significant injury; suicidal or homicidal ideation and aggressive behavior; and specified post-randomization scores on relevant PANSS items. Several PANSS-based criteria require the finding at two consecutive assessments separated by 3-7 days. The total-score thresholds differ according to whether the randomization score was greater than 40 or less than or equal to 40, and the item-score criteria also depend on the maximum baseline score for those items.

A relapse-free endpoint is useful because it captures whether a participant crosses a defined threshold for clinically important deterioration or a serious event over follow-up. It does not describe every aspect of symptoms, functioning, or quality of life. The registry lists symptom and functioning measures as secondary outcomes, including PANSS, Clinical Global Impression Severity, and Personal and Social Performance. The endpoint's meaning therefore rests on the stated event definition and should not be treated as a complete description of all outcomes important to participants.

7. Results Posted in the Registry

• Double Blind: Paliperidone Palmitate 1 Month Formulation: 90.0% (441/490) versus 91.5% (419/458) on control; risk difference -1.5 percentage points (95% CI -5.2 to 2.2), risk ratio 0.98 (0.94–1.02); unadjusted two-proportion z-test p = 0.431.

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.

Percentage of Participants Who Met the Criteria for Symptomatic Remission Based on Andreasen Criteria

• 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:
  • Double Blind: Paliperidone Palmitate 1 Month Formulation: 59.2% (303/512) versus 58.4% (282/483) on control; risk difference 0.8 percentage points (95% CI -5.3 to 6.9), risk ratio 1.01 (0.91–1.12); unadjusted two-proportion z-test p = 0.799.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double Blind: Paliperidone Palmitate 1 Month Formulation and the control. The interval gives the range of effects that remain compatible with the data.

The listed secondary outcomes cover several related but distinct domains: symptom severity, symptom subscales, functioning, and symptomatic remission. This breadth can help describe whether the primary relapse result is accompanied by patterns in other clinical measures. At the same time, these endpoints are not interchangeable. A score change, a remission classification, and remaining free of relapse each capture a different aspect of participants' status and may use different timeframes or analysis populations.

The quantitative secondary comparison available in the registry record is for symptomatic remission based on Andreasen criteria during Weeks 41 to 65. Its recalculated estimate is close to zero, its unadjusted p-value is 0.799, and its confidence interval spans zero. This is broadly consistent with a small observed contrast between groups for that specific secondary measure, but it does not establish equivalence or confirm the primary finding. It also cannot stand in for the other listed secondary outcomes, for which detailed results are not reported in the registry record.

Secondary outcomes generally carry less weight than the primary endpoint when they are not the main basis of the trial's question. If many outcomes are examined, some may appear more unusual by chance alone. A prespecified order of testing or multiplicity adjustment can address this concern, but the registry record does not report the relevant plan or adjustment. The secondary findings should therefore be considered contextual evidence and interpreted with the primary result, rather than treated as a collection of separate definitive tests.

The overall pattern that can be described from the available information is limited: the primary relapse-free percentages are close, and the available remission comparison is also close, with uncertainty spanning no difference. The registry record does not provide enough numerical results to characterize the direction and precision of the full set of symptom and functioning outcomes. Any broader claim about consistency across all secondary endpoints would go beyond what is reported.

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

• Change From Double-Blind (DB) Baseline in Positive and Negative Syndrome Scale (PANSS) Total Score at Week 48
• Change From DB Baseline in Clinical Global Impression Severity (CGI-S) Scale Score at Week 48
• Change From DB Baseline in Personal and Social Performance (PSP) Total Score at Week 48
• Percentage of Participants Who Met the Criteria for Symptomatic Remission Based on Andreasen Criteria
• Change From Baseline in Positive and Negative Syndrome Subscales Score at Week 48
• Change From Baseline in Marder Factor Subscale Score at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons involve a binary endpoint: each analysed participant is classified as without relapse or not without relapse. For a binary outcome, a group percentage is the share of participants in that group who meet the stated classification. The primary outcome is reported as the percentage without relapse, and its group denominators are the participants included in the modified intent-to-treat analysis set. The denominator matters because a percentage describes the analysed group, not necessarily every person enrolled in the trial.

What does the risk difference describe?

The comparison is expressed as a risk difference, which subtracts the event proportion in one group from the event proportion in the other, using a stated group order. Here, the comparison is the 1-month formulation relative to the 3-month formulation, and the outcome is being without relapse. A value at zero corresponds to equal observed proportions; values on either side describe the direction of the difference under that ordering. The registry's comparison estimate is a simple unadjusted recalculation from the posted summary statistics, not a reported adjusted model estimate.

A risk difference is an absolute measure. It describes the gap in proportions rather than a proportional change relative to one group's result. This can make it easier to understand what the comparison means on the outcome's percentage scale. It does not adjust for covariates, account for features of the randomization beyond the group assignment, or replace the trial's planned analysis. The registry record does not report the model or adjustment procedure used in a formal sponsor analysis.

What does the p-value tell a reader?

A p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. A larger p-value is not the probability that the null hypothesis is true, and it does not establish that two treatments have the same effect. In the primary comparison, the posted unadjusted p-value is 0.431. It should be read with the estimated comparison and its confidence interval, not as a stand-alone verdict.

The statistical question in a superiority test is commonly whether the data support a difference from zero. A non-inferiority question is different: it asks whether the result rules out a loss larger than a prespecified margin. The trial title identifies a non-inferiority objective, but the margin and formal analysis details are not reported in the registry record. As a result, the posted p-value for the recalculated unadjusted comparison cannot be treated as the p-value for the trial's formal non-inferiority analysis.

Why use a confidence interval?

A confidence interval gives a range of effect values compatible with the data and the method used to calculate the interval. Its width communicates precision: a narrower interval indicates less sampling uncertainty under the method's assumptions, while a wider interval leaves a broader range of effects plausible. Whether an interval includes zero is relevant to a test of no difference, but the interval must also be considered against a non-inferiority margin for a non-inferiority question. The primary recalculated interval includes zero. The margin needed for a formal non-inferiority interpretation is not reported in the registry record.

Confidence intervals do not account for every source of uncertainty. They reflect sampling variation under the calculation method, but they do not correct for problems such as missing outcome data, deviations from the analysis plan, or selective reporting. The registry record's endpoint description gives the modified intent-to-treat population but does not report the missing-data method, sensitivity analyses, or the handling of participants with incomplete follow-up. Those details are important to evaluating whether the interval captures the uncertainty relevant to the trial's intended claim.

How does the analysis population affect interpretation?

The primary outcome population is defined as participants randomly assigned to treatment during the double-blind phase, who received at least one dose of study drug and had no errors in delivery of active treatment. This is the registry's modified intent-to-treat definition. Randomization is intended to make groups comparable at baseline, but exclusions after randomization can affect that comparability if the excluded participants differ in ways related to treatment or outcome. The registry record does not report how many participants were excluded for each reason, or the results for other analysis populations.

The endpoint group counts are 458 for the 3-month formulation and 490 for the 1-month formulation. These are analysis denominators, not the overall enrollment figure. The registry record does not report a per-protocol analysis, a full intent-to-treat analysis, or sensitivity analyses using alternative population definitions. For a non-inferiority study, the choice of analysis population and consistency across analyses can be particularly important; the available registry information is not sufficient to assess those features.

What can be inferred from the secondary outcome analysis?

The record lists secondary outcomes covering symptom scores, severity ratings, functioning, remission, and symptom subscales. It gives a quantitative comparison for symptomatic remission based on Andreasen criteria. A secondary outcome may provide corroborating or complementary information, but it does not automatically confirm the primary result. The outcome may use a different definition, follow-up window, or analysis population. The registry record does not report the formal statistical plan for the secondary outcomes or a multiplicity adjustment.

When many outcomes are assessed, the chance of finding an apparently notable result by chance can increase. Adjustment procedures can help control this issue, but they may also change how evidence is interpreted. Without a reported hierarchy of outcomes, adjustment method, or complete outcome-specific analyses, secondary findings are best treated as supportive and exploratory rather than as independent confirmation of the primary endpoint.

Overall, the posted results support a descriptive comparison of the observed group proportions and an unadjusted assessment of uncertainty. They do not reveal the trial's complete planned analysis strategy. The statistical methods used for the sponsor's formal non-inferiority conclusion, the handling of missing outcomes, and the prespecified multiplicity procedure are not reported in the registry record.

11. Confidence Intervals and Precision

The primary endpoint percentages are close in the posted results: 91.5% without relapse in the 3-month formulation arm and 90.0% in the 1-month formulation arm. The recalculated confidence interval for the risk difference includes zero. In practical statistical terms, the interval does not isolate a single direction of difference: it remains compatible with no difference as well as with differences in either direction. Its interpretation as evidence for or against non-inferiority would also require the prespecified non-inferiority margin, which is not reported in the registry record.

A confidence interval is more informative than a point estimate alone because it displays uncertainty around the estimated comparison. The point estimate gives one value calculated from the observed data, while the interval shows a range of values that remain compatible with those data under the calculation method. A broad interval implies limited precision; a narrow interval implies greater precision. The registry record reports a recalculated interval for the comparison, but the primary arm-level outcome entries do not report arm-specific confidence limits.

The primary comparison's unadjusted p-value is 0.431. This does not establish equality, and it does not show that an important difference has been excluded. The relevant precision question is whether the interval rules out effects that would matter under the trial's non-inferiority framework. That cannot be judged without the margin and the trial's planned analysis, neither of which is reported in the registry record. The observed percentages should therefore be read as estimates with uncertainty, not as exact underlying event probabilities.

Precision also depends on the analysis population and completeness of follow-up. The registry defines the primary analysis set, but it does not report missing-data methods or sensitivity analyses. An interval calculated from available summaries cannot resolve uncertainty about how incomplete outcome information may have affected the comparison. The result is consequently best understood as a moderately informative descriptive estimate whose formal non-inferiority interpretation remains unresolved 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 planning figures describe participants per arm, not total events. They are illustrations based on the observed primary effect, rather than the original sample-size calculation for this trial. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planning number of participants per arm under which the calculation would have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher chance of detection, so it requires more participants under the same assumptions. These are planning probabilities for a hypothetical future study, not probabilities that the present trial's result is correct.

For the primary endpoint, planning for 100% of the observed effect gives 5,982 participants per arm for 80% power and 8,007 participants per arm for 90% power. Planning for 75% of the observed effect gives 10,442 participants per arm for 80% power and 13,979 participants per arm for 90% power. Planning for 50% of the observed effect gives 23,063 participants per arm for 80% power and 30,874 participants per arm for 90% power. The figures increase as the effect to detect becomes smaller because a smaller separation between groups is harder to distinguish from random variation.

The sample-size curve expresses the same planning relationship across effect sizes: detecting a more modest effect generally requires a larger sample under the stated assumptions. These calculations are not observed power. They are planning illustrations derived from the observed effect, and they should not be interpreted as the power the completed trial actually had or as evidence that the trial was adequately designed for its non-inferiority objective.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.915; treatment proportion p₁ = 0.900; average p̄ = 0.907.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4099 = 0.8034.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4098 = 0.3449.
4. n = (0.8034 + 0.3449)² / (-0.0148)² = 5,981.0, rounded up to 5,982 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 <- 0.914847161572052                          # control proportion
p1 <- 0.9                          # 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(1515423)
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 = 5,982 (80% power), 8,007 (90% power)
 75% of observed effect: n per arm = 10,442 (80% power), 13,979 (90% power)
 50% of observed effect: n per arm = 23,063 (80% power), 30,874 (90% power)
power.prop.test: 5981 
Simulated power at n = 5,982 per arm: 0.802 (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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple endpoints, time points, groups, or statistical comparisons. With more opportunities to test hypotheses, a nominally unusual result can occur by chance even when no corresponding underlying effect exists. A prespecified hierarchy, adjustment method, or clearly defined confirmatory strategy can help explain how the risk of false-positive findings is controlled. The registry record lists several secondary outcomes but does not report a multiplicity plan, an outcome hierarchy, or adjustment procedures.

The primary endpoint is identified, and the official title identifies a non-inferiority objective. However, the registry record does not report the non-inferiority margin, the formal sponsor analysis, or the planned statistical model. It also lists no reported analyses. The unadjusted comparisons available for interpretation are recalculations from the posted summary statistics. They should not be mistaken for the trial's complete confirmatory analysis or for a multiplicity-adjusted result.

Missing data are another important concern for a longitudinal endpoint assessed through Week 48. Participants may have incomplete follow-up or may not have an outcome classification available at the intended assessment. The registry record does not report how missing endpoint data were handled, whether follow-up after treatment discontinuation contributed to the endpoint, or whether sensitivity analyses examined alternative assumptions. These omissions make it difficult to assess how robust the observed proportions are to missingness.

The registry defines the primary modified intent-to-treat set as randomized participants in the double-blind phase who received at least one study-drug dose and had no errors in active-treatment delivery. It does not report the outcome results for a full intent-to-treat population or a per-protocol population. This is relevant because the trial is described as non-inferiority: exclusions or deviations can influence estimates, and agreement across appropriate analysis populations can help assess robustness. The available record does not permit that comparison.

These reporting gaps do not mean that the study necessarily used no multiplicity or missing-data procedures. They mean that such procedures are not reported in the registry record. Interpretation should remain tied to the reported population and the unadjusted summary comparison, without inferring an unreported statistical plan.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: schizophrenia (2.4%), psychotic disorder (1.0%), suicide attempt (0.8%), hallucination, auditory (0.4%), suicidal ideation (0.4%).

The serious adverse event entries use different risk groups for the open-label and double-blind phases. In the open-label paliperidone palmitate 1-month group, the registry reports 101 participants with a serious adverse event among 1429 at risk. In the double-blind 3-month group, it reports 26 among 504 at risk; in the double-blind 1-month group, it reports 37 among 512 at risk. These are counts of participants with reported serious adverse events and the corresponding registry denominators, not exposure-adjusted rates.

The open-label group should not be read as directly interchangeable with either double-blind group. The phases and at-risk populations differ, and the record does not provide a basis for treating the open-label count as a randomized comparison against the double-blind arms. The registry also reports other adverse events separately, with 457 of 1429 in the open-label group, 212 of 504 in the double-blind 3-month group, and 208 of 512 in the double-blind 1-month group.

The listed serious-event terms include schizophrenia at 2.4%, psychotic disorder at 1.0%, suicide attempt at 0.8%, auditory hallucination at 0.4%, suicidal ideation at 0.4%, and psychiatric symptom at 0.4%. These terms describe reported events, not causal conclusions. Death counts are not reported in the registry record. The entries alone do not establish comparative safety, and the registry summary does not provide the detail needed to assess event timing, exposure duration, or attribution.

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

The primary result describes the percentage of analysed participants who met the registry definition of remaining without relapse during the double-blind phase through Week 48. The posted percentages were 91.5% for the 3-month formulation and 90.0% for the 1-month formulation. The unadjusted recalculated comparison has a confidence interval that includes zero, and its p-value is 0.431. Together, these statistics indicate that the observed group percentages were close while leaving uncertainty about the direction and size of the underlying difference.

The result does not prove that the formulations are equivalent. A non-significant difference test is not an equivalence test, and the trial's formal non-inferiority margin is not reported in the registry record. Without that margin and the sponsor's planned analysis, the posted summary cannot establish whether the trial met its non-inferiority objective. A formal conclusion would require an analysis designed to compare the uncertainty interval with the prespecified margin.

The result also does not show that every participant had the same outcome, that treatment effects were identical across subgroups, or that the group percentages apply beyond this study population. The trial concerned participants with schizophrenia who had been stabilized on the 1-month formulation and were randomized during a double-blind phase. Generalizing the result to other populations or treatment contexts would require evidence beyond the information in the registry record.

The endpoint is a composite definition of relapse that includes hospitalization, symptom-score changes, and specified behavioral or safety events. It captures an important aspect of clinical course, but it is not a complete measure of symptoms, functioning, or participants' experience. The registry lists additional symptom and functioning outcomes, yet detailed results for most of those measures are not reported in the record used for this analysis.

Finally, the reported comparison does not settle how missing outcomes, deviations, or multiple outcome testing affected the conclusions. The record does not report the missing-data procedures, multiplicity approach, or full sponsor analysis. The sound interpretation is therefore descriptive and cautious: the posted data show similar observed relapse-free percentages, with uncertainty that does not establish equality or formally resolve non-inferiority.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it frames a comparison around non-inferiority rather than a simple search for evidence that one group differs from another. In a non-inferiority study, the scientific question is whether any possible disadvantage of the new strategy is small enough relative to a prespecified acceptable margin. The estimated difference and its uncertainty must be interpreted against that margin. Although the official title identifies a non-inferiority design, the margin is not reported in the registry record, which limits what can be concluded from the posted numbers.

The endpoint also illustrates how a binary clinical outcome compresses a more complex follow-up history into a participant-level classification. The relapse definition includes hospitalization, changes in PANSS scores, and specified behavioral events. Such a composite can capture several clinically important pathways, but its interpretation depends on the precise event criteria and the time window. Readers should distinguish the percentage without relapse from measures of symptom severity, functioning, or remission.

The analysis highlights why point estimates, p-values, and confidence intervals answer different questions. The percentages describe the observed groups; the p-value summarizes compatibility with a null hypothesis under a test; and the interval displays uncertainty around a recalculated difference. None alone establishes equivalence. The result's statistical meaning depends on the design objective and the prespecified margin, not merely on whether a conventional difference test is statistically notable.

Finally, the record makes visible the importance of reporting analytic details. The modified intent-to-treat population is defined, but the original sample-size justification, missing-data approach, multiplicity plan, and formal analysis results are not reported. Those details are not administrative extras: they determine how the displayed estimates should be connected to the trial's stated objective. This is a useful example of why registry outcome summaries should be interpreted alongside complete methods and analysis reporting when available.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary interpretive limitation is that the registry record identifies a non-inferiority objective but does not report the non-inferiority margin or the formal sponsor analysis. The posted unadjusted recalculation can describe the observed comparison, but it cannot establish that a prespecified non-inferiority criterion was met. The record lists no reported analyses, so the recalculated result should not be presented as the sponsor's definitive inferential result.

The primary endpoint population is a modified intent-to-treat set that excludes participants who did not receive at least one dose or had errors in delivery of active treatment. The record does not provide counts by exclusion reason, results from other analysis populations, or sensitivity analyses. This limits assessment of whether the result is robust to population definition, an important consideration in a non-inferiority design.

The registry does not report how missing Week 48 outcome information was handled, whether participants who discontinued treatment continued to be followed for relapse, or how incomplete assessments affected classification. It also does not report the multiplicity plan for the several secondary outcomes. These gaps prevent a full assessment of missing-data bias and the strength of secondary evidence.

The detailed outcome information available includes the primary relapse-free measure and the symptomatic remission measure, while the broader secondary outcome list includes symptom and functioning measures whose detailed results are not reported in the registry record. This restricts the ability to assess consistency across all clinical domains. Safety entries are reported across open-label and double-blind groups with different at-risk populations, so they should not be treated as a single direct randomized safety comparison. The record also does not report deaths.

The study population was participants with schizophrenia stabilized on the 1-month formulation before the double-blind comparison. The posted results therefore address that study context, not all people with schizophrenia or all treatment settings. The registry record does not provide the details needed to assess external validity beyond the stated population and design.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Paliperidone Palmitate 3 Month and 1 Month Formulations for the Treatment of Patients With Schizophrenia — NCT01515423.
• Registry record last updated 2016-05-02; status last verified 2016-04.
• Results first posted 2016-05-02.
• 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 3 randomized, multicenter, double-blind, parallel-group non-inferiority study of paliperidone palmitate 3-month and 1-month formulations in participants with schizophrenia stabilized on the 1-month formulation. Overall enrollment was 1429. The primary endpoint was the percentage without relapse during the double-blind phase through Week 48.

In the modified intent-to-treat analysis set, the reported relapse-free percentages were 91.5% for the 3-month formulation and 90.0% for the 1-month formulation. The recalculated unadjusted comparison has p = 0.431 and a confidence interval that includes zero. The record does not report the non-inferiority margin, formal sponsor analysis, original sample-size justification, missing-data procedures, or multiplicity plan. The posted figures therefore support a descriptive comparison, but do not by themselves resolve the trial's formal non-inferiority question.