Long-acting Injectable Risperidone in Patients With Schizophrenia After an Acute Episode: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long-acting Injectable Risperidone in Patients With Schizophrenia After an Acute Episode (NCT00216671), a randomized phase 4 study. The primary outcome is Change in Positive And Negative Syndrome Scale (PANSS) Total Score From Baseline to Endpoint.

2. Clinical Question

The study addresses the timing of transition to injectable treatment after an acute episode, rather than a comparison of injectable risperidone with no treatment. Its primary objective was framed as a non-inferiority question. The registry record does not report the non-inferiority margin, so the clinical size of the difference that would have counted as acceptable cannot be assessed from the record.

3. Trial Design

This was a randomized, open-label, parallel-group phase 4 trial. The registry lists an enrollment of 220 and describes the study as completed. Its recorded start was 2005-11 and primary completion was 2009-12. The sponsor was Janssen Pharmaceutica N.V., Belgium. The registry record does not report the method used to generate or conceal the random allocation sequence.

The randomized comparison was early versus routine initiation of Risperdal Consta after an acute episode of schizophrenia. In the early arm, injections were scheduled to begin at baseline; in the routine arm, they were scheduled to begin at week 12. Both arm descriptions state a dose range of 25 mg to 50 mg every 14 days and describe continued oral antipsychotics or risperidone after the first injection, with subsequent tapering. The wording of the tapering descriptions is incomplete in the registry record, and further operational details are not reported in the registry record.

Masking was none. Participants and study personnel therefore were not described as masked to assignment. This matters for outcomes that involve assessment or judgment, even though PANSS is a structured symptom scale. The record does not report details of assessor masking, adherence monitoring, or the management of treatment changes beyond the arm descriptions.

The primary analysis population was per protocol, not all randomized patients. The record states that patients with an eligibility violation or major protocol violation were excluded and gives exclusions by arm; it also notes one early-arm patient without an endpoint PANSS score. The registry record does not report a detailed flow of participants through follow-up or explain how missing endpoint values were handled in the analysis beyond the endpoint definition.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol analysis: all randomized patients who had no violation on eligibility criteria or no major protocol violation. This excluded 42 patients in the early and 34 in the late initiation group. 1 patient in the early initiation group had no PANSS at endpoint. The endpoint is the last post-baseline value of the patient.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change in Positive And Negative Syndrome Scale (PANSS) Total Score From Baseline to Endpoint, measured over at baseline and Week 26 or at premature discontinuation.

The primary endpoint was change in Positive and Negative Syndrome Scale (PANSS) total score from baseline to endpoint. The endpoint time was week 26 or premature discontinuation. The record defines endpoint as the last post-baseline observation, although its detailed wording is truncated. PANSS is a schizophrenia symptom measure comprising 30 items, each scored from 1 (absent) to 7 (extreme), with a total score from 30 to 210.

A change score summarizes how the recorded total differs from baseline, while the endpoint definition allows a participant who discontinues early to contribute a last post-baseline measurement. The reported group summaries are means and standard deviations. The mean change was negative in each arm, indicating that the observed scores were lower at the analysis endpoint than at baseline on average. This description concerns the measured scores; it does not by itself establish a treatment effect or the clinical importance of a difference between arms.

In general, a structured symptom scale offers a consistent way to quantify symptoms across participants and follow-up assessments. Using a change from baseline can account for where participants began, but interpretation depends on the analysis population, the handling of missing measurements, and the comparison between assigned groups. The record reports an ANCOVA non-inferiority analysis as well as the per-protocol arm summaries; the non-inferiority margin and fuller analysis details are not reported in the registry record.

7. Results Posted in the Registry

• Late Initiation of Treatment: mean -37.24 versus -38.37 on control; difference 1.13 (95% CI -6.87 to 9.13), standardized effect d = 0.05; z-test p = 0.782.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in PANSS Total Score at Week 6

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Late Initiation of Treatment: mean -27.96 versus -27.48 on control; difference -0.48 (95% CI -6.97 to 6.01), standardized effect d = -0.03; z-test p = 0.885.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Late Initiation of Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in PANSS Total Score at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Late Initiation of Treatment: mean -34.49 versus -35.84 on control; difference 1.35 (95% CI -6.57 to 9.27), standardized effect d = 0.06; z-test p = 0.738.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Late Initiation of Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Endpoint in Clinical Global Impression - Severity (CGI-S)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Late Initiation of Treatment: mean -2.03 versus -1.91 on control; difference -0.12 (95% CI -0.56 to 0.32), standardized effect d = -0.09; z-test p = 0.591.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Late Initiation of Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted secondary outcomes, the recalculated comparisons generally show small mean differences relative to their uncertainty, and their confidence intervals span no difference. The outcomes cover PANSS change at earlier assessments and changes in clinical severity, functioning, and quality of life. Considered as a group, the pattern does not suggest a clear, consistent separation between early and routine initiation in the reported secondary measures.

This broad pattern is compatible with the primary result, which also does not show a clear average difference in the unadjusted comparison. It should not be used to infer equivalence: the same missing non-inferiority margin that limits interpretation of the primary result also matters here, and secondary outcomes do not replace the primary endpoint. Nor do the secondary findings establish that the strategies have the same effects across symptoms, functioning, and quality of life.

The registry posts multiple secondary outcomes, including repeated PANSS assessments and more than one kind of clinical measure. The record does not report a multiplicity plan or adjustment. In general, examining multiple outcomes creates more opportunities for chance findings, so unadjusted secondary p-values carry less weight than a prespecified, multiplicity-controlled primary analysis. They are best treated as supportive or descriptive evidence rather than as separate confirmatory conclusions.

The registry also reports a Wilcoxon two-sample test for the endpoint CGI-S comparison and a signed-rank test within the early-initiation group. The two-sample test compares groups; the signed-rank test concerns change within one group and does not test whether early initiation differs from routine initiation. These tests do not alter the overall interpretation of the randomized comparison, and the registry record does not report a broader testing hierarchy that would establish their confirmatory status.

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

• Change From Baseline in PANSS Total Score at Week 6
• Change From Baseline in PANSS Total Score at Week 12
• Change From Baseline to Endpoint in Clinical Global Impression - Severity (CGI-S)
• Change From Baseline to Endpoint in Global Assessment of Functioning (GAF)
• Change From Baseline to Endpoint in Quality of Life Questionnaire SF-12

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean change summarize?

The primary outcome is continuous: each participant has a PANSS total score and a change from baseline to endpoint. A mean summarizes the average change among participants included in the arm summary. The standard deviation describes how dispersed individual changes are around that mean. It is not the uncertainty of the mean itself. In general, a mean difference compares the two arm averages, whereas a standard deviation describes participant-to-participant variability within an arm.

The posted recalculation uses the difference between the arm means and an unadjusted standard error based on the group summaries. Its estimate is reported as late initiation minus early initiation. A positive value therefore means the mean change in the late-initiation group is numerically higher than the mean change in the early-initiation group under that contrast. Since changes are negative in both arms, this is a comparison of the size and direction of their recorded changes, not a direct count of participants who improved.

Why is the registry analysis different in form?

The registry reports ANCOVA for the primary outcome. In general, analysis of covariance compares groups while accounting for a baseline measure or other included covariates. Such adjustment can produce an estimate and uncertainty that differ from a simple calculation using only group means and standard deviations. The registry record gives the method and result but does not report the complete model specification, covariates, or other implementation details. Thus, the recalculation is a useful descriptive check, not a substitute for the sponsor’s model-based analysis.

The recalculated p-value is an unadjusted result from a simple two-group comparison. A p-value measures how compatible the observed data are with a specified null model under the assumptions of that test; it is not the probability that the null hypothesis is true. It also does not establish clinical importance. The confidence interval is more informative about the range of differences that remain compatible with the data under the calculation’s assumptions.

What does the non-inferiority label require?

In general, a non-inferiority study asks whether a new or earlier strategy is not worse than a comparator by more than a prespecified acceptable margin. The margin must be chosen before examining the results and interpreted in clinical context. A confidence interval is assessed relative to that margin, with the direction of the contrast made explicit. The registry labels its ANCOVA result as non-inferiority or equivalence, but the margin is not reported in the registry record. It is therefore not possible to verify the formal criterion from the posted result alone. A conventional p-value that is not small is not, by itself, evidence of non-inferiority.

The record describes a per-protocol analysis population for the primary outcome. In general, excluding participants for protocol violations can be relevant in non-inferiority settings because departures from assigned treatment may make groups appear more similar. That is a methodological consideration, not a claim that such bias occurred in this trial. The record does not provide a corresponding intention-to-treat primary result or enough detail to compare analysis populations.

Why do confidence intervals matter?

A confidence interval gives a range of estimates compatible with the observed data under the statistical model and its assumptions. It conveys precision as well as direction. An interval that includes zero means the data do not rule out no average difference at the stated confidence level; it may also include meaningful differences in either direction. It does not establish that all values in the interval are equally likely, nor does it indicate whether any value is clinically acceptable. In a non-inferiority analysis, the relevant comparison is the interval against the prespecified margin, not merely against zero.

General statistical interpretation also depends on assumptions. The simple recalculation treats the outcome as continuous and uses independent groups, with an approximate normal-based comparison. The record posts means and standard deviations, but does not report diagnostic checks for distributional assumptions. ANCOVA has its own modeling assumptions, including an appropriate relationship between baseline and outcome and suitable model specification; the registry record does not provide enough detail to assess those assumptions.

What can the secondary tests establish?

The secondary comparisons are exploratory context unless their status and multiplicity plan are specified. The registry record does not report a multiplicity adjustment or a hierarchy controlling the family of secondary comparisons. When many outcomes or time points are examined, the chance of at least one apparently unusual result can increase. Unadjusted p-values should therefore not be treated as if each were the sole prespecified test. The secondary summaries can indicate whether the outcome pattern broadly accords with the primary result, but they do not independently prove a treatment effect or formal equivalence.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 1.13, with a 95% confidence interval from -6.872 to 9.132. The interval includes zero, so the posted summary statistics are compatible with no average difference under this unadjusted analysis. It also spans values on both sides of zero, so the direction of the underlying difference is not pinned down precisely. The interval should be read as uncertainty about the average contrast, not as a range containing a stated proportion of individual participants’ changes.

The registry ANCOVA result has a 95% confidence interval from -9.24 to 6.99 for its net mean difference. Its direction is reversed relative to the recalculated contrast, and it also includes zero. The two intervals arise from different analyses and should not be combined or treated as interchangeable. The registry record does not give enough model detail to reproduce the ANCOVA interval.

In general, a confidence interval’s width reflects both the variability in the outcome and the amount of information in the analysis, as well as the method used. A broad interval leaves a wider range of possible group differences unresolved. Precision is distinct from whether a result meets a clinical threshold. In a non-inferiority study, the interval must be interpreted relative to the prespecified margin; that margin is not reported in the registry record.

The recalculated interval is based on per-protocol arm summaries, while the registry’s analysis is also reported for the primary comparison. Neither interval alone shows that the two initiation strategies are equivalent. Failure to exclude zero is not a demonstration of no effect, and an estimate close to zero does not guarantee that clinically important differences have been ruled out. The uncertainty should be considered alongside the analysis population, the open-label design, and the unavailable details of missing-data handling.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size display translates the observed recalculated effect into planning illustrations. These figures are participants per arm, not total enrollment or total events. The calculations use two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record, so these planning figures should not be interpreted as the trial’s planned sample size.

The 80% power column describes a planning target under which a study with the stated assumptions would have an 80% chance of detecting the effect being used, if that effect and model assumptions were correct. The 90% power column uses a higher probability target for detecting that same specified effect, and consequently requires a larger planned group size in the displayed calculations. These are prospective design concepts, not evidence about what the completed trial was able to detect.

Rows for planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate how the assumed target changes the required group size. Smaller effects need more participants because they are harder to distinguish from random variation at a given significance level and power target. The observed effect is very small relative to the variability in the primary outcome, which is why the planning illustrations based on it are large. The displayed figures are not observed power; observed power is not a useful substitute for interpreting the estimate and its confidence interval.

These calculations are simplified illustrations rather than a complete protocol design. They do not incorporate trial-specific assumptions that are not reported, such as anticipated attrition, covariate adjustment, a non-inferiority margin, or other design features. They should be read as conditional estimates under the stated planning assumptions, not as a recommendation or a reconstruction of the investigators’ original design.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.130; pooled standard deviation σ = 24.142.
2. n = 2 × (1.96 + 0.842)² × 24.142² / 1.130² = 7,165.2, rounded up to 7,166 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 1.13                      # observed difference in means
sigma <- 24.1420778138064                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(216671)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 7,166 (80% power), 9,593 (90% power)
 75% of observed effect: n per arm = 12,739 (80% power), 17,053 (90% power)
 50% of observed effect: n per arm = 28,661 (80% power), 38,369 (90% power)
power.t.test: 7166.2 
Simulated power at n = 7,166 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s own primary result is an ANCOVA net mean difference of -1.13, with a 95% confidence interval from -9.24 to 6.99 and p = 0.784. It is categorized as a non-inferiority or equivalence analysis. The recalculation from the posted arm means gives a mean difference of 1.13, with a 95% confidence interval from -6.872 to 9.132 and p = 0.782, using late initiation minus early initiation. The opposite signs reflect the contrast direction; the estimates should not be compared without accounting for that direction.

The recalculation is an unadjusted check based on summary statistics, whereas ANCOVA is the registry’s own model-based analysis. The registry result is the appropriate result to cite as the sponsor’s analysis. The small differences between the reported estimates, intervals, and p-values can arise because the methods and contrast conventions differ. The registry record does not report the full ANCOVA specification, so the analysis cannot be independently reconstructed from the record.

The results are broadly consistent in that both intervals include zero and neither analysis establishes a clear average difference from these results alone. However, non-inferiority cannot be confirmed solely from a non-significant comparison or an interval that crosses zero. The margin and related protocol details are not reported in the registry record, so the formal non-inferiority interpretation remains incomplete.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, with additional assessment times for PANSS. It reports multiple analyses. The record does not report whether a formal multiplicity strategy was prespecified, whether the secondary outcomes were organized into a testing hierarchy, or whether any adjustment was applied to secondary comparisons. Without that information, unadjusted secondary p-values should be treated cautiously: testing multiple questions can increase the chance of apparently notable results arising by chance.

The primary objective is described as non-inferiority, but the margin is not reported in the registry record. The record also does not report the full original statistical analysis plan, whether interim analyses were conducted, or the sample-size justification. These details are important to assess whether the reported analyses match the prespecified design and to interpret a non-inferiority claim. They cannot be inferred from the posted outcome summaries.

The primary endpoint population was per protocol. The registry defines it as randomized patients without an eligibility violation or major protocol violation and reports that 42 patients in the early-initiation group and 34 in the late-initiation group were excluded for these reasons. It additionally notes one early-initiation patient without PANSS at endpoint. The registry record does not report a parallel primary intention-to-treat result or provide a full disposition accounting for the endpoint analysis.

The endpoint is described as the last post-baseline observation at week 26 or premature discontinuation, but the registry record’s detailed description is truncated. Further details about how missing endpoint measurements were handled, whether imputation was used, and whether sensitivity analyses were performed are not reported in the registry record. In general, missing-data assumptions can affect estimates, particularly when discontinuation or missingness is related to outcome. The available information does not establish whether that occurred in this trial.

These reporting gaps do not show that the analyses were inappropriate; they limit independent assessment. They are especially consequential for non-inferiority, where population choice, missing-data handling, and the prespecified margin all contribute to interpreting whether the evidence meets the study’s objective.

16. 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 (4.5%), anxiety (3.6%), extrapyramidal disorder (2.7%), schizophrenia, paranoid type (2.7%), suicidal ideation (2.7%).

The registry reports serious adverse events for the early-initiation and late-initiation groups, each with 110 participants at risk. Serious adverse events affected 18 participants in the early group and 22 in the late group. Other adverse events were reported for 58 participants in the early group and 66 in the late group. These are posted event counts and at-risk denominators; they should be read as safety summaries, not as proof that one strategy is safer.

The listed serious-event terms include Schizophrenia (4.5%), Anxiety (3.6%), Extrapyramidal Disorder (2.7%), Schizophrenia, Paranoid Type (2.7%), Suicidal Ideation (2.7%), and Overdose (1.8%). These percentages are registry-listed term frequencies. The record does not provide enough detail to interpret them as comparative risks for each event term, and the listed terms should not be added together because the record does not establish that they are mutually exclusive.

Deaths are not reported in the registry record. More detailed information about event timing, severity, causality assessment, exposure duration, and statistical comparisons is not reported in the registry record. Safety counts are therefore descriptive and should be interpreted alongside the design and completeness of safety follow-up.

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

The posted primary data show substantial mean reductions in PANSS total score from baseline in both per-protocol groups, with a small recalculated difference between their average changes. The unadjusted confidence interval includes no difference and allows values in either direction. The registry’s ANCOVA result also has an interval that includes zero. These analyses do not establish a clear average difference between the strategies on the primary measure.

That finding is not equivalent to proof that early initiation is non-inferior, equivalent, or identical to routine initiation. Formal non-inferiority interpretation requires a prespecified margin and a confidence interval judged against it. The margin is not reported in the registry record. A non-significant result in a conventional comparison cannot establish non-inferiority simply because it fails to show a difference.

The result also does not establish that either treatment strategy is beneficial compared with no treatment or another therapy. Both arms received active treatment strategies, and the posted comparison concerns timing of initiation. The observed within-group score changes are descriptive; without a suitable comparison, they cannot isolate the effect of treatment from other changes over time.

Interpretation is further limited by the open-label design and the per-protocol endpoint population. The registry record does not report a primary intention-to-treat comparison, detailed missing-data methods, or enough information to judge the robustness of the analysis. Secondary outcome findings provide context but are unadjusted and do not resolve these limitations. Safety summaries are also descriptive and do not establish a comparative safety advantage.

In general, statistical uncertainty and clinical importance are different questions. A range of differences can be compatible with the data, while whether those differences matter depends on clinical context and prespecified criteria. The posted results can be described as not showing a clear group difference in the reported analyses, but they do not support a stronger claim of equality or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial is statistically interesting because its central question is explicitly about non-inferiority: whether an earlier start of injectable treatment could be considered not worse than a routine later start. That question cannot be answered by looking only for a statistically significant difference. It requires a prespecified margin and a confidence interval interpreted against that margin. The registry labels its analysis as non-inferiority or equivalence, but the margin is not reported in the registry record, leaving a key part of the intended inference unavailable.

The contrast also illustrates why analysis details matter. The recalculated unadjusted comparison uses posted means and standard deviations, while the registry reports ANCOVA. Both estimates are close in broad terms, but they are methodologically distinct and expressed with opposite contrast directions. Distinguishing the sponsor’s analysis from a simple recalculation prevents an unadjusted summary from being mistaken for the primary model-based result.

Population definition is another important issue. The primary outcome is reported for a per-protocol population, with exclusions for eligibility or major protocol violations. In non-inferiority work, both protocol adherence and missing outcomes can influence apparent similarity. The record does not give a parallel intention-to-treat result or detailed missing-data analyses, so readers cannot assess the stability of the conclusion across populations and assumptions.

Finally, multiple secondary measures can add clinical context, but they need a clear role in the analysis plan. Without a reported multiplicity strategy, secondary p-values are less conclusive. The trial therefore demonstrates the difference between a result that does not show a clear separation and evidence that meets a formal non-inferiority criterion. That distinction is central to sound interpretation of clinical trial statistics.

19. Limitations

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

The registry record leaves several trial-specific details unavailable. The non-inferiority margin is not reported, limiting assessment of whether the confidence interval meets the stated objective. The complete statistical analysis plan, the original sample-size justification, and any interim analyses are not reported in the registry record. The ANCOVA specification and covariates are also not described in enough detail to reproduce the sponsor’s analysis.

The primary endpoint is based on a per-protocol population. Although the record gives the stated reasons and arm-specific exclusions, it does not report a corresponding primary intention-to-treat result. The endpoint description says the last post-baseline observation was used for week 26 or premature discontinuation, but its detail is truncated. Methods for missing data, imputation, and sensitivity analyses are not reported in the registry record.

The study was open-label, and the record does not describe assessor masking. This may matter for a symptom outcome involving assessment. The registry record also does not provide sufficient details to evaluate adherence, treatment exposure over time, or other aspects of implementation beyond the arm descriptions.

Finally, there are multiple secondary measures and analyses, but no multiplicity approach is reported. Secondary findings should therefore be considered descriptive rather than treated as multiple independent confirmations. The safety summaries lack detail on event timing, duration of exposure, and comparative statistical assessment. These limitations constrain interpretation of efficacy, non-inferiority, and safety without demonstrating that the trial’s conduct or analyses were flawed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Long-acting Injectable Risperidone in Patients With Schizophrenia After an Acute Episode — NCT00216671.
• Registry record last updated 2013-07-19; status last verified 2013-07.
• Results first posted 2011-12-02.
• 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.

23. Record Summary

This completed randomized, open-label, parallel-group phase 4 trial compared early with routine initiation of Risperdal Consta after an acute episode of schizophrenia. The primary endpoint was change in PANSS total score from baseline to week 26 or premature discontinuation, analyzed in a per-protocol population.

The recalculated unadjusted mean difference was 1.13, with a 95% confidence interval from -6.872 to 9.132. The registry’s ANCOVA result was -1.13, with a 95% confidence interval from -9.24 to 6.99. Both intervals include zero, but the non-inferiority margin is not reported in the registry record, so formal non-inferiority cannot be verified from the posted information. Secondary outcomes broadly show no clear separation, while multiplicity and missing-data details are unavailable. Safety figures are descriptive.