Study of the Safety, Tolerability, and Pharmacokinetics of Once Weekly Zicronapine in Patients With Schizophrenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of the Safety, Tolerability, and Pharmacokinetics of Once Weekly Zicronapine in Patients With Schizophrenia (NCT01377233), a randomized phase 2 study. The primary outcome is Number of Patients With Adverse Events as a Measure of Safety and Tolerability.

2. Clinical Question

The registry describes a randomized, double-blind, parallel-group, explorative study comparing daily dosing with once-weekly dosing of zicronapine. The principal safety question is whether the number of participants with treatment-emergent adverse events differed across the reported dosing groups. The posted outcome gives counts of participants with events, while the comparison estimates express differences in event risk.

The design included an open-label period before the randomized, double-blind period. All 46 enrolled patients contributed to the reported open-label arm. Of those patients, 42 were subsequently randomized across four arms: daily zicronapine and three once-weekly doses. This distinction matters when reading comparisons because the open-label group represents an earlier study period, whereas the other groups represent randomized treatment arms. The registry’s listed comparisons use the open-label group as the control.

Safety and tolerability are the focus of the primary outcome. The record also lists changes in Positive and Negative Syndrome Scale totals and subscales, Clinical Global Impression Severity, and Clinical Global Impression Improvement as secondary outcomes. It does not post analyses for those secondary outcomes, so the registry record does not establish what those measures showed.

3. Trial Design

This was a Phase 2, randomized, quadruple-masked, parallel-group study sponsored by H. Lundbeck A/S. The title describes an explorative comparison of daily and weekly zicronapine dosing in patients with schizophrenia. The registry marks the study completed. The recorded start was 2011-07 and primary completion was 2012-02.

The study had an open-label lead-in using zicronapine 10 mg daily. The primary outcome description specifies an open-label period of 3 weeks post-baseline plus 8 weeks of safety follow-up, for 11 weeks total. It also specifies a double-blind period of 5 weeks post-randomization plus 8 weeks of safety follow-up, for 13 weeks total. Adverse events from the open-label period are reported for 46 patients. After that period, 42 patients were randomized to four groups: 10 mg daily, 20 mg once weekly, 30 mg once weekly, or 45 mg once weekly.

The randomized arm sizes were 11, 10, 11, and 10 participants, respectively. The registry does not give further arm descriptions. Although the study is described as quadruple-masked, the specific parties who were masked are not reported in the registry record. The method used to generate the random allocation sequence and the procedure used to conceal allocation are also not reported in the registry record.

The open-label group and randomized groups represent different study periods, and their reported follow-up windows differ. The randomized comparison is therefore the relevant setting for interpreting differences among the daily and weekly arms, while the listed calculations compare each randomized arm with the open-label group. That feature warrants caution when treating the posted comparisons as direct randomized treatment contrasts. Further details about the planned analysis, including any adjustment for period or other variables, are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 46 patients were initially enrolled in a 3-week open-label study period. The 42 patients who completed the open-label period were subsequently randomized to a 5-week double-blind period.

Open-label

Reasons for not completing this period:

Double-blind

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Adverse events for the 46 patients enrolled in the open-label period are reported in the first (open-label) study arm. Adverse events for the 42 patients (out of the 46 enrolled) who were subsequently randomized to the double-blind period are reported across the last four (randomized) study arms.

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: Baseline characteristics for the 4 patients enrolled in the open-label period but not randomized to the double blinded period, are reported in the first (open-label) study arm. Baseline characteristics for the 42 patients who were subsequently randomized to the double-blind period are reported across the last four (randomized) study arms.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients With Adverse Events as a Measure of Safety and Tolerability, measured over 11 weeks for open-label period; 13 weeks for double-blind period.

The primary endpoint counts participants with treatment-emergent adverse events as a measure of safety and tolerability. It reports the number of patients with events during each of the study periods and their corresponding safety follow-up. The open-label period covers 11 weeks in total; the double-blind period covers 13 weeks in total, according to the endpoint description.

A participant count is an intuitive way to describe how many people experienced an event, rather than how many separate event episodes occurred. It is a binary outcome at the participant level: each person is classified according to whether an event was reported. This allows event occurrence to be compared across groups, but the count alone does not describe the number, duration, severity, or clinical importance of events experienced by each participant. Those details require additional outcome reporting.

The endpoint is used because the study’s stated purpose is to evaluate safety, tolerability, and pharmacokinetics of once-weekly dosing compared with daily dosing. The posted primary outcome specifically addresses adverse events; it is not a measure of symptom improvement. The registry lists symptom and clinical-global-impression measures as secondary outcomes, but does not post their analyses.

Exposure time and study period are relevant to interpretation. The open-label and double-blind periods have different durations and occur at different stages of the study. The event counts should therefore be understood in relation to their stated periods, rather than as if they all arose from one common follow-up window.

7. Results Posted in the Registry

• Zicronapine Basis Dose 10 mg Daily: 72.7% (8/11) versus 26.1% (12/46) on control; risk difference 46.6 percentage points (95% CI 17.4 to 75.9), risk ratio 2.79 (1.52–5.11); unadjusted two-proportion z-test p = 0.004.
• Zicronapine Low Dose 20 mg Once Weekly: 40.0% (4/10) versus 26.1% (12/46) on control; risk difference 13.9 percentage points (95% CI -19.0 to 46.8), risk ratio 1.53 (0.62–3.78); unadjusted two-proportion z-test p = 0.377.
• Zicronapine Med Dose 30 mg Once Weekly: 36.4% (4/11) versus 26.1% (12/46) on control; risk difference 10.3 percentage points (95% CI -20.9 to 41.4), risk ratio 1.39 (0.56–3.50); unadjusted two-proportion z-test p = 0.496.
• Zicronapine High Dose 45 mg Once Weekly: 90.0% (9/10) versus 26.1% (12/46) on control; risk difference 63.9 percentage points (95% CI 41.4 to 86.4), risk ratio 3.45 (2.03–5.85); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a participant-level binary measure: whether a patient had at least one treatment-emergent adverse event during the relevant period. For a binary outcome, each participant contributes to the event count or does not. The reported counts can be expressed as risks, meaning the proportion of participants in a group who experienced an event. The comparison results present a risk difference, which is the difference between the two group risks.

A risk difference is on an absolute scale. A positive estimate in the posted comparisons means the risk in the randomized arm is higher than the risk in the open-label control, as reflected by the reported group risks. For example, the comparison for randomized 10 mg daily gives a risk difference of 0.466. This estimate should be read with its confidence interval, not in isolation. The registry’s comparisons also list risk ratios and odds ratios, but the risk-difference scale makes the absolute contrast explicit.

The comparison estimates and p-values are unadjusted. An unadjusted comparison considers each listed contrast without an adjustment for testing multiple comparisons. When several comparisons are made, the chance of at least one apparently unusual result can increase. Whether and how the trial team planned to address multiple comparisons is not reported in the registry record. The posted p-values should therefore be interpreted as individual, unadjusted results rather than as results from a documented multiplicity-controlled testing strategy.

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. 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 for the 45 mg comparison is reported as <0.001; the p-values for the other comparisons are also posted. The registry record does not identify the test used to obtain these p-values, so the exact test procedure and its assumptions are not reported in the registry record.

The confidence intervals give a range of effect estimates compatible with the data under the interval method’s assumptions. A narrow interval indicates greater precision than a wide interval, while a wide interval indicates substantial uncertainty about the effect’s magnitude. For a risk difference, an interval that includes zero is compatible with no difference as well as with differences in either direction. The intervals for the 20 mg and 30 mg comparisons include zero; the intervals for the 10 mg daily and 45 mg weekly comparisons do not.

The groups are small, particularly the randomized arms. In small groups, individual outcomes have considerable influence on the estimated risk. As a result, differences in a few participants can lead to substantial shifts in estimates. The intervals are accordingly important for conveying uncertainty, rather than relying only on whether an unadjusted p-value passes a threshold.

What does the comparison actually contrast?

The listed risk-difference calculations compare each randomized arm with the open-label 10 mg daily arm. The open-label observations were collected earlier in the study, before the randomized double-blind period. The groups therefore differ not only in assigned dose and schedule, but also in study period and follow-up window. A straightforward group contrast does not by itself separate these features. The registry record does not report a model that adjusts for period or other participant characteristics.

Within the randomized period, the 10 mg daily group is a randomized arm alongside the weekly-dose arms. A contrast using that concurrent randomized group would answer a different comparison question from the posted calculations using the open-label group. The record does not post those alternative comparisons. The randomized allocation may support treatment comparisons within the randomized phase, but the details needed to evaluate the allocation and planned analysis are not reported in the registry record.

Why can over-dispersion matter?

Over-dispersion is a general statistical issue in count models: observed variability can exceed what a model assumes. It matters when outcomes are counts of events or event episodes and a model relies on a particular variance structure. The primary endpoint is a count of participants with at least one event, not a reported count of all event episodes. The registry does not report an over-dispersion model or a count-model analysis, so this issue should not be imputed to the posted primary comparisons.

The record lists four outcome measures and three secondary outcomes, but no posted analyses. The methods used for those secondary outcomes, handling of repeated measures, missing observations, covariate adjustment, and analysis populations are not reported in the registry record. It is also not reported whether any interim analyses were planned or conducted. These omissions limit the ability to reconstruct a full prespecified analysis plan from the registry results.

10. Confidence Intervals and Precision

Precision is reflected in the confidence intervals around the risk differences. For the comparison with randomized 10 mg daily, the estimate is 0.466 and the interval runs from 0.174 to 0.759. For 20 mg once weekly, the estimate is 0.139 and the interval runs from -0.19 to 0.468. For 30 mg once weekly, the estimate is 0.103 and the interval runs from -0.208 to 0.414. For 45 mg once weekly, the estimate is 0.639 and the interval runs from 0.414 to 0.864.

The intervals for 20 mg and 30 mg span zero, indicating that the posted data are compatible with no risk difference as well as with differences in either direction. Their breadth also allows for effects that could be meaningfully different in magnitude. The intervals for randomized 10 mg daily and 45 mg weekly lie above zero, but they still cover a range of possible differences. A point estimate is not a precise description of the true effect when the interval remains broad.

Small randomized groups contribute to uncertainty. The weekly-dose arms have 10, 11, and 10 participants, and the daily randomized arm has 11. With these group sizes, the event status of a small number of participants can appreciably affect the estimated risks. The open-label group is larger, with 46 patients, but that does not remove uncertainty or resolve the difference in study period between the control observations and randomized observations.

The registry does not state the confidence-interval method, so the exact method and its assumptions are not reported in the registry record. The intervals are useful for judging the range of statistical uncertainty, but they do not account automatically for every design limitation, such as the use of an earlier open-label control group, possible missing data, or unreported analysis choices.

11. Planning a Similar Trial: Sample Size

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

The sample-size display gives planning illustrations based on the observed risk differences. Its figures are participants per arm, not total event counts. Each row considers planning for the full observed effect, 75% of the observed effect, or 50% of the observed effect. The smaller-effect scenarios require more participants per arm than the larger-effect scenarios. This is a general feature of power planning: when the effect to be detected is smaller, it is harder to distinguish from random variation, so a larger sample is needed under otherwise comparable assumptions.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original trial’s own sample-size justification and design assumptions are not reported in the registry record. These calculations use the observed effects as planning inputs and should not be read as the trial’s original design rationale.

The 80% power column gives the illustrative number of participants per arm associated with an 80% probability of detecting the specified effect under the planning assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding participant count for a higher planned probability of detection. These are prospective planning quantities, not descriptions of what happened in the completed study. They are not observed power.

The estimates differ substantially by comparison because the observed effects differ. For example, planning for 50% of the observed effect gives 67 participants per arm for the randomized daily comparison, 675 for 20 mg weekly, 1,215 for 30 mg weekly, and 37 for 45 mg weekly at 80% power. These are illustrative calculations from the posted effects, not recommendations or evidence that the underlying effects will reproduce. The sample-size curve should be read in the same planning context: it describes how the required sample changes with the assumed effect size, not the precision achieved by the enrolled trial.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.261; treatment proportion p₁ = 0.727; average p̄ = 0.494.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3858.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6254 = 0.5264.
4. n = (1.3858 + 0.5264)² / (0.4664)² = 16.8, rounded up to 17 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 <- 0.260869565217391                          # control proportion
p1 <- 0.727272727272727                          # 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(1377233)
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 = 17 (80% power), 22 (90% power)
 75% of observed effect: n per arm = 31 (80% power), 41 (90% power)
 50% of observed effect: n per arm = 67 (80% power), 89 (90% power)
power.prop.test: 16.8 
Simulated power at n = 17 per arm: 0.828 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists three secondary outcomes: Positive and Negative Syndrome Scale total and subscale change from baseline, Clinical Global Impression Severity change from baseline, and Clinical Global Impression Improvement. Although the record identifies these measures, it does not post analyses for them. Their results, effect estimates, confidence intervals, and p-values are therefore not reported in the registry record.

Multiplicity arises when many outcomes or comparisons are examined. If each is tested separately without adjustment, the overall chance of at least one false-positive finding can be greater than for a single test. There are four posted pairwise comparisons using the open-label control group, and their p-values are unadjusted. A family-wise adjustment, hierarchical strategy, or other multiplicity procedure is not reported in the registry record. Consequently, the posted p-values should not be treated as if a documented correction for multiple comparisons had been applied.

Missing-data handling is not reported in the registry record. The record does not say whether participants with incomplete outcome information were excluded, whether missing outcomes were imputed, or whether sensitivity analyses were conducted. The counts describe the reported participants in the named groups, but the available record does not establish how any missing observations were treated.

The analysis populations are also not described in detail. The registry says that 46 patients enrolled in the open-label period and 42 were subsequently randomized. It does not specify whether analyses followed intention-to-treat, per-protocol, safety, or another population definition. It does not report whether any randomized participants discontinued or were excluded from the outcome summaries.

The original statistical analysis plan, any interim analyses, and the planned approach to multiplicity are not reported in the registry record. Without those details, it is not possible to determine whether the posted analyses match a prespecified plan or whether additional analyses were performed but not posted. These absences affect interpretation of the results and are distinct from the numerical uncertainty represented by the confidence intervals.

14. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: schizophrenia (10.0%), pulmonary embolism (10.0%).

The serious adverse event summary reports the number of participants at risk and the number affected in each group. It lists no serious adverse event participants in the open-label group of 46 or in the randomized daily group of 11. It reports one affected participant among 10 assigned to 20 mg weekly, one among 11 assigned to 30 mg weekly, and one among 10 assigned to 45 mg weekly. These counts describe participants with serious adverse events, not necessarily the total number of serious event episodes.

The registry lists Schizophrenia and Pulmonary Embolism as top serious adverse event terms, each reported as 10.0%. The posted record does not establish the arm attribution or provide enough event-level information to interpret these terms further. Death counts are not reported in the registry record.

Serious adverse events are distinct from the primary endpoint’s broader count of participants with treatment-emergent adverse events. For example, the randomized 45 mg weekly arm has 9 participants with adverse events in the primary outcome, while the serious-event summary reports 1 participant affected. These measures should not be conflated: serious-event counts capture a more specific safety category, while the primary outcome includes treatment-emergent events more broadly. The registry provides no further detail on event severity classifications, timing, relatedness, or outcomes.

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

The results describe adverse events reported during an open-label period and a subsequent randomized, double-blind period. The counts show that the number of participants with reported events varied across the groups. The risk-difference estimates and their confidence intervals quantify the posted comparisons with the open-label group, while also showing considerable uncertainty in several contrasts.

These findings do not establish whether zicronapine is clinically beneficial or harmful. The primary endpoint is safety and tolerability, and the registry does not post analyses for its listed symptom and clinical-global-impression secondary outcomes. Nor do the event counts by themselves indicate the clinical importance of the events. Information about event type, severity, duration, and relationship to treatment is not sufficiently detailed in the posted primary results.

The comparisons should not be interpreted as clean randomized contrasts against a concurrent control, because the posted control group comes from the open-label period before randomization. The groups also have different stated follow-up windows. Those design features can complicate attribution of differences to dose or dosing schedule. The registry record does not report analyses addressing period differences or other potential sources of imbalance.

The comparisons are unadjusted, and the analysis plan, missing-data approach, and multiplicity strategy are not reported in the registry record. The confidence intervals communicate statistical uncertainty for the posted estimates, but do not resolve these design and reporting limitations. The modest sizes of the randomized groups also mean that the estimates can be sensitive to the outcomes of a small number of participants.

The defensible interpretation is therefore descriptive and limited to the registry results: the record reports specific participant counts and unadjusted risk differences, with intervals that vary in width and include zero for two comparisons. It does not support a broad conclusion about treatment effects beyond those posted safety summaries.

16. Why This Trial Matters Statistically

This study illustrates why the structure of a trial matters as much as the numerical comparison. The record contains both an open-label lead-in and a randomized period. Although the posted calculations compare each randomized group with the open-label group, those observations were collected at different stages and under different follow-up windows. A numerical contrast does not, by itself, make the groups exchangeable or isolate a dosing effect.

It also demonstrates the importance of reporting absolute event measures alongside uncertainty. Participant counts and risk differences help readers understand the scale of the observed safety outcomes. Confidence intervals show that similar-looking estimates can remain uncertain, particularly when randomized groups are small. A p-value alone cannot communicate the possible range of effect sizes or their practical meaning.

The study is described as explorative, and the randomized sample is limited. Explorative results can help characterize the evidence and motivate careful future investigation, but estimates from small groups may be unstable. The planning illustrations make the dependence of required sample size on assumed effect magnitude visible: planning for a smaller fraction of an observed effect entails larger participant requirements.

Finally, the record highlights the difference between registering outcomes and posting their analyses. Several symptom-related secondary outcomes are named, but their results are not posted. Clear reporting of analysis populations, missing-data handling, multiplicity decisions, and methods would help readers distinguish confirmatory evidence from exploratory comparisons. Those details are not reported in the registry record, so interpretation must remain tied to the outcomes and calculations that are posted.

17. Limitations

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

Several limitations specific to this trial affect interpretation. The principal comparison calculations use the open-label 10 mg daily group as control, even though the four comparison groups belong to the later randomized period. The open-label group and randomized arms also have different follow-up windows. This means the posted contrasts do not represent straightforward concurrent randomized comparisons, and the record does not report an adjustment for these differences.

The randomized groups are small, with 10 or 11 participants each. The resulting estimates may be sensitive to a small number of participant outcomes, and several confidence intervals are broad. The sample-size calculations are retrospective planning illustrations based on observed effects, not evidence that the trial was designed with those assumptions or achieved a particular probability of detecting an effect.

Reporting is incomplete for several interpretive details. The methods for randomization and allocation concealment, the specific masking roles, the statistical tests, the confidence-interval method, analysis populations, missing-data handling, interim analyses, and the original sample-size rationale are not reported in the registry record. The registry lists secondary symptom outcomes but does not post their analyses, and it does not report an adjustment strategy for multiple comparisons.

The primary outcome provides participant counts rather than a detailed account of each event. Event-level descriptions, severity, duration, timing, attribution, and outcome are not reported in the primary results. For serious events, the registry lists top terms but does not provide enough information to attribute them to a particular group. Death counts are not reported in the registry record. These gaps prevent a complete characterization of safety from the posted summaries alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Study of the Safety, Tolerability, and Pharmacokinetics of Once Weekly Zicronapine in Patients With Schizophrenia — NCT01377233.
• Registry record last updated 2016-03-22; status last verified 2016-02.
• Results first posted 2016-03-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT01377233 is a completed Phase 2 randomized, quadruple-masked, parallel-group, explorative study of daily and once-weekly zicronapine in patients with schizophrenia. H. Lundbeck A/S is listed as sponsor. The registry records the study start as 2011-07 and primary completion as 2012-02.

The primary outcome counts participants with treatment-emergent adverse events during an open-label period and a later double-blind period. There were 46 patients in the open-label period and 42 subsequently randomized across daily dosing and three once-weekly dose groups. The posted comparisons use the open-label group as control and report unadjusted risk differences with confidence intervals and p-values.

The record also lists three secondary outcomes, but does not post their analyses. Details of the original statistical plan, missing-data methods, and several other analysis procedures are not reported in the registry record. The results are therefore best read as limited safety summaries and exploratory comparisons, with attention to the different study periods, small randomized groups, and uncertainty in the estimates.