Efficacy of an Early Antipsychotic Switch in Case of Poor Initial Response to the Treatment of Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of an Early Antipsychotic Switch in Case of Poor Initial Response to the Treatment of Schizophrenia (NCT01029769), a randomized na study. The primary outcome is Number of Patients in Symptomatic Remission at Week 8 Comparing the "Switched" With the "Non Switched" Early Non-responders.

2. Clinical Question

The trial’s stated hypothesis was that switching after two weeks would be followed by more frequent symptomatic remission at week 8 than continued treatment among patients who had not responded early. This is a question about the comparative outcomes of two treatment strategies within a defined subgroup, not a comparison of all randomized participants by initial drug assignment. The registry record notes that initial medication groups were combined for the primary endpoint analysis according to early non-response status and later switch status.

3. Trial Design

The registry record describes a randomized, triple-masked, crossover trial with planned enrollment of 350 participants. The phase is listed as not applicable. The conditions listed are schizophrenia, schizoaffective disorder, and schizophreniform disorder. The sponsor is Technical University of Munich. The record lists the trial as completed, with a start date of 2009-12 and primary completion in 2014-03.

The treatment sequence had an initial two-week period using olanzapine or amisulpride, followed by an extended six-week treatment period. Early responders and early non-responders were distinguished after the initial period. The primary comparison is restricted to early non-responders: one group switched medication and the other did not. The endpoint is assessed at week 8. The primary analysis combined patients across the initial medication assignments and compared groups according to their early response and switching status.

The record’s crossover designation is part of the registered design, but the full sequence and allocation details are not reported in the registry record. The arm descriptions are blank, so the precise medication sequence within each primary-analysis group is not reported in the registry record. The number randomized to each initial medication, the number meeting early non-response criteria, and the disposition of participants between trial periods are also not reported in the registry record. The analysis groups contain 60 participants who switched and 55 who did not switch; the record does not explain how these analysis-group counts relate to all enrolled participants.

Randomization and triple masking describe design features, but the registry record does not report who was masked or how masking was maintained. Nor does it report details of allocation concealment or the trial’s original statistical design assumptions. These omissions limit how fully the registered design can be reconstructed from the record alone.

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: The enrollment at baseline comprises the periods "initial olanzapine" and "initial amisulpride"; a re-randomisation was performed after 2 weeks of treatment; the patient numbers in the second phase of the trial must not be added to the overall participant number at baseline (other three groups all formed in phase II of the trial); NOTE that the groups "early responders", "early non-responders switched", "early non-responders non-switched" become active only in phase II of the trial, not before!!

Period 1: Initial 2-week Treatment

Period 2: Extended 6-week Treatment

Analysis population for the primary outcome, as defined in the registry: please note that all patients, regardless of the medication received, were combined in these groups for the primary endpoint analysis solely depending on whether they have met the criteria for "early non-response" at the end of phase I of the trial; so the statistical analysis does not follow the treatment arms in phase I of the trial (patients received alternatively olanzapine or amisulpride, but both types of treatment appear in one and the same analysis group!)

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: Three hundred and twenty-seven patients were randomized in study phase I.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients in Symptomatic Remission at Week 8 Comparing the "Switched" With the "Non Switched" Early Non-responders, measured over 8 weeks.

The primary endpoint is the number of participants in symptomatic remission at week 8, comparing early non-responders who switched with early non-responders who did not switch. It is a binary outcome: each participant is classified as in remission or not in remission. The registry definition requires a rating of 3 or less on each of eight PANSS items: delusions, unusual thought content, hallucinatory behavior, conceptual disorganization, mannerisms or posturing, blunted affect, social withdrawal, and lack of spontaneity. A rating above 3 on any one item means the participant is classified as not in remission.

A binary remission outcome translates several symptom ratings into a clinically interpretable status at a specified assessment time. It asks whether all listed symptom criteria are met, rather than how much the total symptom score changed on average. Because every listed item must satisfy the threshold, a participant can be classified as not in remission even if other items improve. The endpoint therefore captures a particular threshold-based outcome, not every dimension of symptom change.

The registry record also lists PANSS total score change as a secondary outcome. That measure describes change on a continuous scale and complements, rather than duplicates, the remission classification. The registry record does not report further detail about the timing or handling of missing primary endpoint assessments.

7. Results Posted in the Registry

• Early Non-responders Non-switched: 45.5% (25/55) versus 68.3% (41/60) on control; risk difference -22.9 percentage points (95% CI -40.5 to -5.2), risk ratio 0.67 (0.47–0.93); unadjusted two-proportion z-test p = 0.013.

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.

PANSS Total Score Change

• 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:
  • Ealy Non-responders Non-switched: mean -17.30 versus -22.80 on control; difference 5.50 (95% CI -0.92 to 11.92), standardized effect d = 0.31; z-test p = 0.093.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ealy Non-responders Non-switched and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: PANSS total score change at 8 weeks. The posted secondary summaries and the primary remission comparison represent different aspects of symptom outcome. One is a change in total score; the other is a binary status requiring all eight specified items to meet a threshold. They need not move in lockstep, and a difference in one outcome does not automatically establish a corresponding difference in the other.

Across the posted endpoints, the primary remission comparison has an unadjusted interval that excludes zero, whereas the secondary mean-difference interval includes zero. The secondary result is less decisive about the direction and size of a mean change under its unadjusted calculation. This contrast is not inherently contradictory: outcome definitions, scales, and statistical precision differ. It also does not establish that one endpoint is more valid; the registry record identifies remission as primary and PANSS total score change as secondary.

Secondary outcomes generally carry less confirmatory weight when multiple outcomes are examined without a reported plan to control the chance of false-positive findings. The registry record does not report whether multiplicity adjustment was used, nor does it provide a fuller hierarchy of secondary analyses. Thus the secondary result is best read as additional, supportive context rather than as an independent confirmation of the primary comparison. No other secondary endpoint results are posted in the registry record.

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

• PANSS Total Score Change

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either meets the remission definition or does not. The registry reports counts and group sizes, and the recalculated comparison uses those posted summaries without adjustment. This makes the calculation transparent, but it does not incorporate covariates, stratification, or other features that might have been used in the trial’s analysis. The sponsor’s reported method is logistic regression, with p = 0.01. The registry record does not provide its regression coefficient, confidence interval, covariates, or full model specification.

What does a risk difference describe?

A risk difference compares the proportions of participants with an outcome in two groups by subtracting one group’s proportion from the other. Its scale is an absolute difference in outcome probability. A value of zero would represent equal observed proportions. The sign depends on which group is subtracted from which, so the group order must be read carefully. In this comparison, the recalculated estimate is expressed as non-switched minus switched; its negative sign corresponds to fewer observed remissions in the non-switched group.

General statistical explanation: a risk difference is often useful when the practical question concerns the absolute separation between outcome rates. It is different from a risk ratio or odds ratio, which express relative comparisons. Those relative measures can make an identical absolute difference appear larger or smaller depending on the baseline outcome frequency. The registry-derived summaries include relative measures as well, but the central interpretation rests on the risk difference and its interval.

What does the confidence interval add?

A confidence interval expresses sampling uncertainty around an estimate under the assumptions of its calculation. A narrower interval indicates greater precision, while a wider interval indicates less precision. The primary interval extends from -0.405 to -0.052 for the non-switched-minus-switched risk difference. It stays on the negative side of zero, which is consistent with the unadjusted p-value of 0.013. The interval does not measure every form of uncertainty: it does not, by itself, address bias from missing outcomes, errors in outcome classification, or differences between the analysis groups that were not handled by the calculation.

General statistical explanation: a p-value evaluates how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-value of 0.013 belongs to the unadjusted recalculation. The sponsor’s logistic regression p-value is separately reported as 0.01; the record does not provide enough model detail to establish whether the two analyses used identical assumptions.

Why does over-dispersion matter?

Over-dispersion is a general concern when observed variability in data is greater than a statistical model expects. It can lead to uncertainty being understated if the model treats observations as more independent or less variable than they are. The primary endpoint is a participant-level binary outcome, but the registry record does not report a diagnostic assessment of over-dispersion or model-fit details. No conclusion about whether it affected the sponsor analysis can be drawn from the registry record.

How should the secondary continuous outcome be understood?

PANSS total score change is reported as a mean with a standard deviation for each group. A mean summarizes the average change, while a standard deviation describes the spread of individual changes around that average. The recalculated mean difference compares the group averages. Its interval includes zero, so the posted unadjusted summary is compatible with both a difference in either direction and no mean difference under the calculation’s assumptions. This does not establish equivalence or show that the groups have identical outcomes.

The registry lists a mean difference of 5.5, a confidence interval from -0.925 to 11.92, and p = 0.093 for the unadjusted recalculation. Those statistics answer a different question from the remission endpoint: average score change rather than the proportion crossing a multi-item remission threshold. Differences in scale and definition mean that the primary and secondary outcomes need not have the same statistical pattern.

What is and is not known about the analysis?

The record reports a logistic regression analysis for the primary comparison but does not provide the model’s effect estimate, uncertainty interval, included covariates, or missing-data procedure. It reports one analysis and two outcome measures. Details of interim analyses, prespecified analysis populations, multiplicity control, and the original statistical plan are not reported in the registry record. The unadjusted recalculations should therefore be treated as descriptive checks based on posted summary statistics, not as replacements for the sponsor’s analysis or as a reconstruction of the full protocol analysis.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference interval runs from -0.405 to -0.052, using the comparison order non-switched minus switched. Its placement below zero indicates that the observed proportions favored the switched group in this unadjusted comparison. The interval’s width reflects uncertainty from the available analysis-group sizes and observed counts. It excludes zero, while still spanning a range of possible absolute differences rather than identifying a single exact effect.

Confidence intervals are not guarantees that the true value lies within a particular interval, and they do not account for every possible source of error. Their interpretation depends on the statistical method and assumptions. Here, the interval is based on the posted group summaries and is not the confidence interval from the sponsor’s logistic regression, which is not reported in the registry record. The sponsor’s reported p-value is available, but its estimated effect and precision are not.

For the secondary mean difference, the interval extends from -0.925 to 11.92 and includes zero. This indicates less decisive evidence about the direction of the mean difference under the unadjusted calculation. It does not prove that the groups are equivalent. Both endpoints have uncertainty, but their scales and definitions differ, so their intervals should not be compared as though they measured the same quantity.

More precise conclusions would require additional information that is not reported in the registry record, including the complete analysis population, missing outcome handling, and the sponsor model’s effect estimate and confidence interval. The posted counts and group summaries allow a transparent unadjusted comparison, but do not remove uncertainty about trial conduct or analysis choices.

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 figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. The registry record does not report the assumptions used to plan the original trial’s enrollment.

For the primary binary comparison, figures refer to participants per arm, not total events. The entries are 73 participants per arm for 80% power and 97 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 128 and 170 participants per arm. For 50% of the observed effect, they are 280 and 374 participants per arm.

For the secondary continuous outcome, the entries are also participants per arm. They range from 164 and 220 participants per arm for planning at 100% of the observed effect, to 292 and 390 for 75%, and 656 and 878 for 50%.

In plain language, the 80% power column gives the planned number per arm for a study with an 80% chance of detecting the stated effect under the listed assumptions; the 90% column does the same for a 90% chance. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants as the target effect gets smaller. These figures are not observed power: they are hypothetical planning values, not a measure of the probability that this completed trial detected its effect.

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 = 0.683; treatment proportion p₁ = 0.455; average p̄ = 0.569.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7004 = 1.3727.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6814 = 0.5735.
4. n = (1.3727 + 0.5735)² / (-0.2288)² = 72.4, rounded up to 73 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 <- 0.683333333333333                          # control proportion
p1 <- 0.454545454545455                          # 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(1029769)
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 = 73 (80% power), 97 (90% power)
 75% of observed effect: n per arm = 128 (80% power), 170 (90% power)
 50% of observed effect: n per arm = 280 (80% power), 374 (90% power)
power.prop.test: 72.4 
Simulated power at n = 73 per arm: 0.814 (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 logistic regression, with p = 0.01. It does not report the regression estimate, confidence interval, model covariates, or further specification. The unadjusted recalculation uses the posted remission counts and group sizes and gives p = 0.013, with a risk difference expressed as non-switched minus switched. These are related but not identical summaries: logistic regression models the binary outcome, while the recalculation compares the proportions directly without adjustment.

The sponsor’s own analysis takes precedence over the recalculation as the trial’s reported analysis. The recalculation is useful as a straightforward check of the posted counts, but cannot reproduce or replace a model whose specification is not reported. The registry record does not indicate a discrepancy between the sponsor’s result and the recalculated result. The similar p-values should not be interpreted as proof that the analyses used the same assumptions or produced the same effect estimate.

Because the sponsor’s effect estimate and uncertainty interval are absent, its p-value alone does not convey the estimated size or precision of the modeled association. The posted counts and unadjusted interval add descriptive information, while the record leaves the full relationship between the modeled and unadjusted analyses incompletely documented.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies symptomatic remission at week 8 as the primary endpoint and PANSS total score change as a secondary outcome. It also lists two outcome measures and one analysis. The record does not report whether the outcome hierarchy was prespecified in a statistical analysis plan, whether any multiplicity adjustment was applied, or how conclusions were to be drawn across outcomes. Without that information, the unadjusted p-values should not be treated as though they necessarily account for all testing performed.

Multiplicity matters because examining several outcomes or analyses can increase the chance that at least one result appears statistically unusual by chance. General statistical explanation: adjustment procedures can address this issue, but may also change the threshold or interpretation for individual results. No adjustment method or rationale is reported in the registry record, so it is not possible to say whether the posted p-values are adjusted.

Information about missing data is also limited. The posted primary groups include 60 participants who switched and 55 who did not, but the registry record does not describe the number with missing week-8 remission assessments, the rules for classifying missing outcomes, or whether an imputation method was used. The corresponding details for the PANSS score change are not reported in the registry record. These omissions make it difficult to determine whether the posted analyses include every participant assigned to the relevant groups.

The record’s primary-analysis description says that patients were combined across medication received and classified according to early non-response and switching status. The full analysis population, handling of protocol deviations, and rules for entry into each analysis are not reported in the registry record. Interim analyses, stopping rules, and other planned analyses are also not reported in the registry record. These gaps limit assessment of whether the analyses followed prespecified procedures and how missingness or multiple testing might affect the apparent strength of evidence.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalisation (4.3%), prolongation of hospitalisation (1.8%), life threatening event (1.4%), death (0.6%).

Serious adverse events are reported for several treatment-period groups. During the initial two-week treatment period, the registry lists 3 serious adverse events among 163 participants treated with amisulpride and 3 among 164 treated with olanzapine. During the extended six-week period, the listed counts are 7 among 140 early responders, 5 among 70 early non-responders who switched, and 4 among 72 early non-responders who did not switch. Deaths are listed as 0, 1, 1, 0, and 0, respectively, across those five groups.

The registry also identifies hospitalisation (4.3%), prolongation of hospitalisation (1.8%), life threatening event (1.4%), and death (0.6%) among the leading serious-event terms. These figures describe the posted safety record and should be read alongside the treatment-period grouping. Participants are counted in groups defined by period and response status, and the groups do not constitute a single direct randomized comparison of switch versus no switch for every safety outcome. The record does not provide further detail about event relatedness, overlap between terms, or the statistical comparison of safety groups.

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

The posted primary results show that symptomatic remission at week 8 was observed in 41 of 60 early non-responders who switched and 25 of 55 who did not switch. The unadjusted comparison estimates a lower remission proportion in the non-switched group, with a confidence interval that remains below zero for the non-switched-minus-switched difference. The sponsor’s reported logistic regression analysis has p = 0.01. Together, these are evidence of a difference in the posted primary analysis groups, but they do not resolve every question about the size, durability, or cause of that difference.

The results do not describe all trial participants as one population-level comparison. The primary analysis is restricted to early non-responders and combines participants across initial medication assignments. It is not a direct estimate of the effect of a specific named drug, nor does it report outcomes for every possible treatment sequence. The registry record’s arm descriptions are blank and its primary population description is truncated, limiting reconstruction of the exact analysis population.

The results do not establish that every early non-responder would have the same outcome, or that a future study would produce the same estimate. A confidence interval represents sampling uncertainty under the calculation’s assumptions, while missing-data practices, model details, and other possible sources of uncertainty are not fully described. The secondary score-change result has an interval including zero and should not be treated as proof of no difference or as a substitute for the primary outcome.

Statistical significance is not the same as clinical importance. The registry record does not state a threshold for a clinically important difference in remission, nor does it report a patient-level interpretation of the score change. The observed comparison is therefore best understood as a statistical summary of the trial’s posted analysis groups, not a universal forecast or an individual treatment recommendation.

18. Why This Trial Matters Statistically

This trial raises a design and analysis question that is common in clinical research: whether an early response assessment can identify a subgroup for whom a change in treatment strategy is worth comparing with continued treatment. The primary question is not simply which initial medication performs better. It asks how outcomes differ among people classified as early non-responders, after grouping them according to whether they switched or stayed on the same medication.

That focus makes the analysis population central to interpretation. Randomization is listed for the trial, but the primary comparison uses groups defined after the initial treatment period. Understanding how participants entered those groups, how the crossover sequences were assigned, and how the analysis handled all randomized participants would help readers assess the comparison. Those details are not fully reported in the registry record.

The endpoint also illustrates a useful distinction between threshold-based and continuous outcomes. Symptomatic remission requires every specified PANSS item to satisfy the criterion, while total score change summarizes average movement across the scale. The two measures can give complementary perspectives, and their statistical uncertainty need not be the same.

Finally, the record makes visible the difference between a sponsor-reported model and a transparent recalculation from counts. The reported logistic regression p-value is the sponsor’s analysis; the unadjusted risk difference and interval provide a direct summary of the posted counts. Reading both responsibly requires attention to what each method estimates and what methodological details remain unavailable.

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.

Several trial-specific limitations arise from the level of detail in the registry record. The primary outcome groups contain 60 switched participants and 55 non-switched participants, while planned enrollment is 350. The record does not explain the participant flow from enrollment to these analysis groups, how many participants were assigned to each original treatment sequence, or why some enrolled participants are not represented in the primary comparison. No reason for the difference can be inferred from the posted information.

The analysis is based on early non-responders and combines participants across the initial medication assignments. This may be appropriate to the stated primary question, but it means the posted result is not a simple comparison of all randomized participants by original assignment. The registry record does not provide enough detail to evaluate the complete randomization-based analysis, the crossover sequence, or potential period and carryover considerations. Specific handling of those design features is not reported in the registry record.

The primary endpoint’s remission rule is explicit, but the record does not report how missing item ratings or incomplete assessments were handled. It also does not report the full model specification behind the sponsor’s logistic regression, an effect estimate and interval for that model, or whether multiple testing was controlled. The description of the primary analysis population is truncated, and the registered arm descriptions are blank.

Safety information is grouped by treatment period and clinical response category. The registry record does not report event attribution or a direct statistical comparison of the safety groups. These limitations concern what can be established from the registry record; they do not demonstrate that a particular design or analysis procedure was or was not used.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy of an Early Antipsychotic Switch in Case of Poor Initial Response to the Treatment of Schizophrenia — NCT01029769.
• Registry record last updated 2024-10-21; status last verified 2015-05.
• Results first posted 2024-10-21.
• 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

The registry record describes NCT01029769, a completed randomized, triple-masked crossover trial sponsored by Technical University of Munich. Planned enrollment was 350, and the listed conditions were schizophrenia, schizoaffective disorder, and schizophreniform disorder. Initial treatment involved olanzapine or amisulpride, followed by an extended treatment period.

The primary endpoint was symptomatic remission at week 8 among early non-responders, comparing those who switched with those who did not. The posted counts were 41 of 60 in the switched group and 25 of 55 in the non-switched group. The sponsor reported logistic regression with p = 0.01; an unadjusted recalculation gives a risk difference of -0.229 for non-switched minus switched, with an interval from -0.405 to -0.052 and p = 0.013.

PANSS total score change was listed as a secondary outcome. Important details about participant flow, missing data, the full statistical model, multiplicity, and the original design assumptions are not reported in the registry record.