A Study of Risperidone Long-Acting Injection Versus Oral Antipsychotics in Schizophrenia Participants With a History of Being Poorly Compliant With Taking Their Medication: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Risperidone Long-Acting Injection Versus Oral Antipsychotics in Schizophrenia Participants With a History of Being Poorly Compliant With Taking Their Medication (NCT00256997), a randomized phase 4 study. The primary outcome is Percentage of Participants Who Experienced a Clinical Exacerbation From Month 3 Post-Randomization.

2. Clinical Question

The question is about the frequency of a broad clinical endpoint in a population selected for a history of poor adherence. It is not limited to hospitalization or a single symptom measure: the registry definition also includes treatment changes, emergency care, self-injury, suicidal ideation, use of treatment-team services, violent behavior, and an increase in antipsychotic dose because of poor symptom control. The recorded outcome therefore combines events that may differ in seriousness and in how they are identified.

The comparison is between assigned treatment strategies in a routine-care setting, not between a medication and no treatment. The registry does not report a blinding procedure; masking is listed as none. The trial was terminated, and the primary outcome description says it was stopped due to futility. Those details warrant care in interpreting the posted estimates, but do not by themselves specify how the futility decision was made or what clinical conclusion should follow.

3. Trial Design

The registry describes a randomized, parallel-group phase 4 trial with no masking. Its official title characterizes the study as pragmatic and conducted in a routine-care setting. It compared risperidone long-acting injection with oral atypical antipsychotics in participants with schizophrenia and a history of poor adherence. The registry records enrollment of 167 participants and identifies Janssen-Ortho Inc., Canada as the sponsor.

In the injection group, risperidone was administered intramuscularly every 2 weeks at an investigator-selected dose of 25 mg, 37.5 mg, or 50 mg. An oral atypical antipsychotic was also used during the first 3 weeks following a dose increase. The description of this arm ends with an incomplete word in the registry record, so further details of its intended duration are not reported there. In the oral-treatment group, an atypical antipsychotic was used according to local label practice for 24 months, with switching to another oral atypical therapy permitted at the investigator’s discretion.

The recorded start was 2006-01 and primary completion was 2009-04. The study status is terminated. The primary outcome description states that the study was stopped due to futility and cautions that utilization of the data requires care. The registry does not report the original sample-size justification, the planned treatment duration for the injection arm, or the criteria and process used to stop the study. Randomization methods and allocation concealment details are not reported in the registry record.

The primary analysis population is described as the intent-to-treat population, defined in the record as participants who received medication and had at least one post-baseline effectiveness measure. That definition should be retained when interpreting the results; it is not a description of every person randomized irrespective of post-baseline assessment. The registry does not report the number of randomized participants excluded from this population, if any, or how missing outcome information was handled.

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: Intent-to-treat (ITT) population included all participants who received medication with at least one post-baseline effectiveness measure. This study was stopped due to futility; care must be exercised in any interpretation of utilization of these data.

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: Out of a total of 167 participants, Baseline data was available for only 165 participants who were included in intent to treat (ITT) population.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Experienced a Clinical Exacerbation From Month 3 Post-Randomization, measured over Month 3 up to Month 24.

The primary endpoint is the percentage of participants who experienced a clinical exacerbation from Month 3 up to Month 24. The registry defines an exacerbation using a broad set of events: hospitalization because of schizophrenia, a change from the current antipsychotic or initiation of an adjunctive antipsychotic, a 2-point worsening in Clinical Global Impression of Severity, an emergency room visit, deliberate self-injury, emergence of clinically significant suicidal ideation, use of treatment-team services, violent behavior, or an increase in the existing antipsychotic dose because of poor symptom control.

This type of endpoint is used to capture clinically consequential deterioration or escalation of care across more than one form of event. In a routine-care comparison, combining events can reflect a wider range of ways that worsening may be recognized and managed. At the same time, the component events are not interchangeable: they differ in severity, clinical meaning, and reliance on decisions by participants or care teams. The overall percentage does not reveal which components contributed to the result unless component-specific results are reported.

The primary time window starts at Month 3 rather than baseline and continues up to Month 24. The reason for selecting that window is not reported in the registry record. The endpoint is a participant-level percentage, not a rate of recurrent exacerbations. The record does not provide component-specific counts, adjudication procedures, or details of how an event was confirmed.

7. Results Posted in the Registry

• Oral Atypical Antipsychotic: 43.0% (37/86) versus 48.1% (38/79) on control; risk difference -5.1 percentage points (95% CI -20.3 to 10.1), risk ratio 0.89 (0.64–1.25); unadjusted two-proportion z-test p = 0.513.

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 Experienced a Clinical Exacerbation

• 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:
  • Oral Atypical Antipsychotic: 54.7% (47/86) versus 54.4% (43/79) on control; risk difference 0.2 percentage points (95% CI -15.0 to 15.4), risk ratio 1.00 (0.76–1.33); unadjusted two-proportion z-test p = 0.977.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oral Atypical Antipsychotic and the control. The interval gives the range of effects that remain compatible with the data.

Time to First Clinical Exacerbation

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Oral Atypical Antipsychotic: mean 11.20 versus 10.40 on control; difference 0.80 (95% CI -1.60 to 3.20), standardized effect d = 0.10; z-test p = 0.514.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oral Atypical Antipsychotic and the control. The interval gives the range of effects that remain compatible with the data.

The registry names secondary outcomes covering clinical exacerbation over a broader time window, time to first exacerbation, symptomatic remission, symptom-scale change, clinical global impressions, resource use, and quality of life. The numerical secondary summaries available for interpretation include a percentage outcome and a time-to-first-event summary. Their recalculated confidence intervals include no difference, so they do not provide a clear separation between the treatment groups. Taken together, the available numerical summaries do not establish a consistent pattern of marked differences across outcomes.

These secondary outcomes address related but distinct questions. An outcome covering a broader interval can differ from the primary outcome’s window; time to first event emphasizes timing; symptom, global-impression, resource-use, and quality-of-life measures capture other dimensions. They may help describe the trial, but they do not replace the prespecified primary endpoint or resolve its uncertainty. Numerical results for the other named secondary outcomes are not reported in the registry record.

Unadjusted secondary comparisons carry less weight when many outcomes are examined. General: looking across multiple outcomes increases the chance that some results may appear notable by chance alone, even when there is no underlying difference. A prespecified approach to multiplicity can address that issue, but such an approach is not reported in the registry record. The termination for futility and the caution attached to interpretation of the data also counsel against drawing a broad conclusion from selected secondary findings.

The secondary outcomes should therefore be read as supporting context rather than as independent confirmation of a treatment advantage or equivalence. Their role is limited by incomplete numerical reporting, uncertainty in the available comparisons, and the lack of a reported multiplicity strategy.

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

• Percentage of Participants Who Experienced a Clinical Exacerbation
• Time to First Clinical Exacerbation
• Time in Symptomatic (Having Symptoms) Remission
• Change From Baseline in Positive and Negative Syndrome Scale (PANSS) - Total Score at Month 24
• Number of Participants With Clinical Global Impression of Severity (CGI-S)
• Number of Participants With Clinical Global Impression of Change (CGI-C)
• Number of Participants With Response to Resource Utilization Questionnaire (RUQ)
• Change From Baseline in Assessment of Quality of Life (AQoL) Score at Month 24

9. Statistical Interpretation

10. Statistical Methods Explained

The following explanations describe general statistical ideas and how they relate to the analyses recorded for this trial. The registry does not report every detail of the statistical plan, so the distinctions below should not be taken as a reconstruction of unreported methods.

What does a risk difference describe?

General: a risk difference compares the proportions of participants with an event in two groups. Its sign depends on the subtraction order. In this comparison, the recalculated estimate is expressed as oral treatment minus risperidone long-acting injection, and is -0.051. A value below zero means the observed event proportion was lower in the oral group on that scale. The estimate is unadjusted: it is calculated from the posted group summaries and does not account for covariates or event timing.

The percentages reported for the primary endpoint are 48.1% for the injection group and 43.0% for the oral group. The recalculated risk difference is a separate representation of the contrast, rather than an additional outcome. Because the values are rounded, the displayed percentages and the recalculated estimate need not reproduce each other exactly if a reader tries to derive one from the other.

What does the confidence interval add?

General: a confidence interval describes uncertainty around an estimated effect under the method’s assumptions. It is not a range containing a fixed proportion of individual participant outcomes, and it does not assign a probability to a particular effect after the data are observed. For the recalculated primary risk difference, the 95% interval is -0.203 to 0.101. Since that interval includes zero, the summary is compatible with no difference as well as with differences in either direction. Its span also indicates that the estimate is not precise enough to rule out potentially meaningful contrasts on the risk-difference scale.

Why is the sponsor analysis different?

The sponsor reports a Cox proportional hazard model with p = 0.550. General: time-to-event methods use information about when an event occurs and can account for participants whose event time is not observed through the full follow-up, subject to the method’s assumptions. A binary risk comparison instead records whether an event occurred during the specified window. These approaches answer related but distinct questions and need not yield identical p-values. The sponsor’s reported p-value does not include an effect estimate or interval in the registry record, so it cannot be used to assess the model-based magnitude or precision from the posted information.

The registry does not report the Cox model’s covariates, checks of the proportional-hazards assumption, handling of censoring, or the exact analysis population for that model. Those details matter for evaluating the fit and interpretation of a time-to-event analysis. The recalculated risk comparison is not a substitute for those missing details or for the sponsor’s own model.

Why can a broad endpoint be difficult to interpret?

General: a composite endpoint combines multiple events into a single summary. This can increase the range of clinically relevant events represented, but the overall result can be driven by components that differ substantially in seriousness or frequency. For this trial, the definition includes hospitalization, treatment changes, symptom worsening, emergency care, and several behavioral or service-use events. The registry does not provide component-level results or describe adjudication, so the total percentage cannot show which kinds of events account for the group summaries.

The endpoint is expressed as a percentage of participants with an event over a defined follow-up window. It does not convey the number of events per participant, the timing of the event, or whether participants experienced repeated events. The separate time-to-first-exacerbation outcome is conceptually different because it concerns time until an initial event, but its posted summary does not supply the sponsor-model estimate or detailed event-time analysis.

What can a p-value establish?

General: a p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The recalculated primary p-value is 0.513, and the sponsor-reported model p-value is 0.550. Neither should be interpreted in isolation from the effect estimate, interval, analysis method, and trial’s termination context. The registry does not report a prespecified multiplicity strategy or a complete statistical analysis plan.

The primary outcome description identifies an intent-to-treat population as participants who received medication and had at least one post-baseline effectiveness measure. General: restricting a population based on post-randomization information can differ from an analysis of every randomized participant, and missing outcome data can affect estimates. The record does not explain how missingness was handled or whether sensitivity analyses were conducted. Thus, the available population definition and summary results do not support a full assessment of possible missing-data effects.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.051, with a 95% confidence interval from -0.203 to 0.101. The interval includes zero and reaches in both directions from the point estimate. This means the posted summary does not pin down the direction of the underlying difference with precision. It is compatible with a lower event proportion in the oral group, little or no difference, or a lower proportion in the injection group, within the interval and the assumptions of the calculation.

General: confidence intervals help distinguish the point estimate from the range of values that remain reasonably compatible with the data under a statistical model. Wider intervals indicate less precision than narrower intervals on the same scale. An interval that includes no difference does not prove that groups are identical; it indicates that the data do not clearly separate the estimate from no difference at the interval’s confidence level.

The reported group percentages are 48.1% for risperidone long-acting injection and 43.0% for oral atypical antipsychotic. The registry does not provide confidence intervals for those group percentages, and the sponsor’s Cox analysis is reported only with p = 0.550. Consequently, the precision of the sponsor’s time-to-event effect estimate cannot be evaluated from the reported model result.

The recalculated interval is based on posted summary statistics and is unadjusted. It does not represent adjustment for baseline characteristics, follow-up time, or potential missingness. The trial’s termination due to futility and the registry’s caution about interpreting utilization of these data are additional reasons to avoid treating the point estimate as a precise or definitive answer.

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 are illustrations based on the observed effect, not a report of the trial’s original design calculation. For the primary binary endpoint, the figures are participants per arm, not total participants or total events. The assumptions recorded for these illustrations 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 80% power column describes the planned number of participants per arm that would, under those assumptions and for the selected effect size, give an 80% chance of detecting that effect using the stated significance level. The 90% power column uses a higher target chance of detecting the selected effect and therefore requires a larger planning sample. These are design calculations, not a description of what happened in the trial.

The rows for 100%, 75%, and 50% of the observed effect explore progressively smaller effects relative to the observed estimate. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under the same assumptions. For the primary endpoint, the listed planning figures rise as the assumed effect gets smaller. Because the observed primary estimate is uncertain, basing a future design directly on it is itself uncertain; the illustrations do not establish a reliable target effect.

Time-to-event planning figures, where applicable, are reported as total numbers of events under the Schoenfeld approach; other planning figures are participants per arm. The primary endpoint figures are of the latter kind. These values are not observed power: observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

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 = 0.481; treatment proportion p₁ = 0.430; average p̄ = 0.456.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7043 = 1.3804.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7034 = 0.5920.
4. n = (1.3804 + 0.5920)² / (-0.0508)² = 1,508.7, rounded up to 1,509 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 <- 0.481012658227848                          # control proportion
p1 <- 0.430232558139535                          # 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(256997)
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 = 1,509 (80% power), 2,020 (90% power)
 75% of observed effect: n per arm = 2,689 (80% power), 3,600 (90% power)
 50% of observed effect: n per arm = 6,063 (80% power), 8,115 (90% power)
power.prop.test: 1508.7 
Simulated power at n = 1,509 per arm: 0.804 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Cox proportional hazard model comparing the two treatment groups, with p = 0.550. It does not report an effect estimate or confidence interval for that model. The recalculated comparison uses the posted event percentages and gives an unadjusted risk difference of -0.051, with a 95% confidence interval from -0.203 to 0.101 and p = 0.513.

These results should not be treated as competing estimates of exactly the same quantity. The Cox model is a time-to-event analysis, while the recalculation compares whether participants experienced an event during the stated period. They use different information and methods, so their p-values can differ without either being a transcription error. The registry does not provide enough detail to reproduce the Cox analysis or compare its underlying effect estimate directly with the risk difference.

The record indicates no discrepancy between the sponsor-reported result and the recalculation. The sponsor’s analysis remains the reported model-based analysis; the recalculation is a simple unadjusted check based on posted summary statistics. Neither p-value establishes equivalence, and the absence of a reported sponsor-model interval limits assessment of its precision.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, but a multiplicity-adjustment plan is not reported in the registry record. General: when analyses cover multiple outcomes or multiple comparisons, the chance of obtaining at least one apparently unusual result by chance can increase. Prespecified methods can limit that risk or clarify which comparisons are confirmatory and which are exploratory. Without a reported plan, unadjusted secondary p-values should be interpreted cautiously and should not be treated as if each were the sole planned test.

The record reports one sponsor analysis for the primary endpoint, using a Cox proportional hazard model. It does not report the full statistical analysis plan, model covariates, model diagnostics, handling of censoring, or whether the analysis was prespecified in the form reported. A formal interim-analysis plan is not reported. Although the primary outcome description says the study was stopped due to futility, that statement alone does not establish whether formal interim analyses occurred, what stopping boundaries were used, or how the decision was reached.

The stated intent-to-treat population consists of participants who received medication and had at least one post-baseline effectiveness measure. This is the registry’s definition and should not be silently replaced with a broader or narrower population. The record does not say how many participants were randomized but lacked a qualifying post-baseline measure, how missing endpoint data were handled, or whether sensitivity analyses assessed the effect of missingness.

General: missing outcome data can affect a group comparison if availability of outcomes is related to treatment or to the outcome itself. The direction and magnitude of any such effect cannot be inferred without further information. The registry also does not report details of adherence to assigned therapy, treatment discontinuation, or outcome ascertainment across the follow-up window. These omissions limit assessment of analysis assumptions and robustness; they do not establish that a particular bias occurred.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina pectoris (2.5%), chest pain (2.5%), dehydration (2.5%), acute coronary syndrome (1.2%), myocardial infarction (1.2%).

The registry reports serious adverse events among participants at risk in each safety group. In the risperidone long-acting injection group, 14 of 81 participants at risk were affected by serious adverse events. In the oral atypical antipsychotic group, 6 of 86 participants at risk were affected. Other adverse events were reported for 70 of 81 participants at risk in the injection group and 69 of 86 in the oral group. These are separate safety summaries and should not be combined or interpreted as a formal comparative analysis.

The listed serious-event terms include angina pectoris, chest pain, and dehydration at 2.5% each, and acute coronary syndrome, myocardial infarction, and abdominal pain at 1.2% each. The record does not establish that these terms represent all serious events, nor does it provide the circumstances, duration, outcome, or causal assessment for each event. Deaths are not reported in the registry record.

General: adverse-event counts and percentages describe events recorded during a study; by themselves, they do not establish that a treatment caused an event or that the groups differ reliably in safety. The safety denominators are not the same as the primary efficacy denominators, and the registry does not report a statistical comparison or adjustment for exposure time. The figures should be read descriptively and in the context of these reporting limits.

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

The primary data describe the percentage of participants with a broadly defined clinical exacerbation during the stated follow-up window. The observed percentages were 48.1% for risperidone long-acting injection and 43.0% for oral atypical antipsychotic. The unadjusted recalculated risk difference has a confidence interval that includes no difference and values in both directions. The result therefore does not provide a precise estimate of which group had a lower event proportion in the population represented by the trial.

That uncertainty does not mean the treatments are proven equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether differences fall within it; such a margin or equivalence analysis is not reported in the registry record. Nor does the result establish that one strategy is superior. The sponsor’s Cox model also reports no statistically clear difference by its p-value, but the model estimate and its precision are not reported.

The endpoint combines diverse clinical events and treatment decisions, and component-specific results are not reported. The group-level percentage cannot reveal whether the observed events were mostly hospitalizations, symptom worsening, treatment changes, or another component. The registry’s population definition, missing-data details, and analysis plan also limit what can be inferred about robustness.

The study was terminated and the primary outcome description states it was stopped for futility, with a caution about interpretation of the data. The record does not explain the decision process, so the termination should be treated as relevant context rather than as a substitute for the reported estimates. These results describe this trial’s posted data; they should not be converted into advice about treatment choice or generalized beyond the trial’s population and setting without additional evidence.

18. Why This Trial Matters Statistically

This trial raises a statistically important question about how to compare treatment strategies in a population with a history of poor medication adherence. Its pragmatic, routine-care framing and allowance for investigator-directed treatment choices place the comparison in a setting where management may be flexible. Such flexibility can make the treatment strategies clinically recognizable, while also making the contrast dependent on decisions made during care.

The primary outcome is not a narrow symptom score. It combines hospitalization, changes in medication, worsening in clinical severity, emergency care, and other events. This breadth matters statistically because a composite can capture different forms of deterioration, but the total result may conceal which components drive the group percentages. Without component-specific results, the overall estimate cannot be decomposed.

The trial also illustrates why an effect estimate and its uncertainty are more informative than a p-value alone. The recalculated risk difference is accompanied by an interval extending across no difference, while the sponsor’s time-to-event analysis is reported with a p-value but no effect estimate or interval. Those summaries answer related but distinct statistical questions and do not establish equivalence.

Finally, termination for futility is important context, but the registry does not report the analysis plan or decision procedure. The posted results therefore require cautious interpretation. They show how incomplete reporting of analysis details, missing-data methods, and multiplicity plans can limit the conclusions readers can draw even when group summaries and a primary model p-value are available.

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

The registry record leaves important trial-specific details unreported. The method of random sequence generation and allocation concealment is not described. Masking is listed as none, so the comparison was open-label; the record does not explain whether outcome assessment was conducted independently of treatment knowledge. This matters particularly for a composite endpoint that includes care decisions and service use.

The primary endpoint includes varied events, but component-level results and event-adjudication procedures are not reported. The registry also does not explain why the primary risk window begins at Month 3, or how the reported analysis treated participants who changed treatment, discontinued, or had incomplete follow-up. These details are relevant to interpreting an outcome that depends partly on treatment changes and events observed over time.

The primary population definition requires receipt of medication and at least one post-baseline effectiveness measure. The registry does not report the numbers or characteristics of participants excluded from that definition, nor the handling of missing outcomes. This prevents a direct assessment of how the analysis population relates to all randomized participants.

The sponsor’s Cox model is reported without an effect estimate, confidence interval, covariate details, censoring procedures, or diagnostic information. The multiplicity plan, interim-analysis procedures, and original sample-size justification are also not reported. The study was terminated after being stopped for futility, but the registry does not provide the timing, criteria, or supporting analysis for that decision. These limitations constrain interpretation; they do not show that any particular analysis choice or bias changed the result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Risperidone Long-Acting Injection Versus Oral Antipsychotics in Schizophrenia Participants With a History of Being Poorly Compliant With Taking Their Medication — NCT00256997.
• Registry record last updated 2013-12-05; status last verified 2013-11.
• Results first posted 2013-10-07.
• 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 randomized, open-label, parallel-group phase 4 trial compared risperidone long-acting injection with oral atypical antipsychotics in participants with schizophrenia and a history of poor medication adherence. The registry records enrollment of 167 participants and identifies the study status as terminated.

The primary endpoint was the percentage experiencing a clinical exacerbation from Month 3 up to Month 24. The registry reports 48.1% in the injection group and 43.0% in the oral group. The unadjusted recalculated risk difference is -0.051, with a 95% confidence interval from -0.203 to 0.101. The sponsor reports a Cox proportional hazard model p-value of 0.550, without an effect estimate or confidence interval.

The primary outcome description says the trial was stopped due to futility and cautions that utilization of the data requires care. Missing-data handling, multiplicity procedures, the original sample-size justification, and the futility decision process are not reported in the registry record.