A Phase 2 Dose Escalating Study to Evaluate the Safety and Efficacy of CB-03-01 Cream in Subjects With Facial Acne Vulgaris: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 2 Dose Escalating Study to Evaluate the Safety and Efficacy of CB-03-01 Cream in Subjects With Facial Acne Vulgaris (NCT01631474), a randomized phase 2 study. The primary outcome is Investigator's Global Assessment (IGA) "Success" - Week 12.

2. Clinical Question

3. Trial Design

The registry record describes a completed Phase 2, multicenter, randomized, double-blind, vehicle-controlled, parallel-group study of CB-03-01 cream for facial acne vulgaris. It lists enrollment of 363 and identifies Intrepid Therapeutics, Inc. as sponsor. The recorded study start is 2012-06 and primary completion is 2014-02. The record describes treatment over 12 weeks in the official title.

Participants were assigned to four active regimens or a vehicle group: 0.1% CB-03-01 twice daily, 0.5% twice daily, 1% once daily, 1% twice daily, or vehicle once or twice daily. The study is described as randomized and double-blind, with parallel groups. The registry record does not report the randomization procedure, allocation concealment details, or how blinding was maintained.

The main efficacy outcome was IGA “success” at Week 12. Its posted population was per protocol, not all enrolled participants: it included eligible members of the ITT population who completed the end-of-study visit and applied at least 80% of expected applications. Group denominators for this outcome range from 52 to 64. Those counts are distinct from the safety group denominators, which range from 70 to 76.

Other listed outcomes include lesion counts, percent change in lesion counts, and IGA outcomes at earlier time points. The registry record does not report the trial’s original sample-size justification, the planned statistical analysis, or whether interim analyses were conducted. The posted material identifies the design and endpoint, but does not establish what analyses were prespecified or how all randomized participants were handled in the original analysis.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-Protocol Population, defined as a subset of the ITT population and included those subjects that met eligibility criteria, completed the end-of-study visit, and applied at least 80% of the expected treatment applications.

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: ITT Population. The ITT population included all subjects enrolled in the study who were randomized and dispensed test article.

6. Primary Endpoint

The registry lists the primary outcome as Investigator's Global Assessment (IGA) "Success" - Week 12, measured over Baseline and Week 12.

The primary outcome is the count of participants who met the study’s definition of IGA “success” at Week 12. The definition required both a final IGA score of clear or almost clear—scores 0 or 1—and an improvement of at least two grades from baseline on the five-point scale from 0=clear to 4=severe. The endpoint is reported as participants, with a count for each treatment group.

This kind of combined endpoint is used to describe how many participants reach a specified clinical assessment state while also showing improvement from their starting score. Requiring both elements makes the outcome more specific than simply counting everyone who is clear or almost clear at the end, or everyone whose score improved by a given amount. It is a binary outcome for each participant: the participant either meets the success definition or does not.

The endpoint was assessed at baseline and Week 12. Its analysis population was the per-protocol population, defined by eligibility, completion of the end-of-study visit, and at least 80% of expected treatment applications. Consequently, the posted counts describe this selected population rather than all enrolled participants. The registry record does not report how missing Week 12 assessments were handled, nor whether the endpoint was analyzed in any additional population.

An IGA success count is a measure of the specified assessment outcome; by itself, it does not describe every aspect of acne severity, individual experience, or safety. Interpretation also depends on the comparison between groups and the uncertainty around that comparison.

7. Results Posted in the Registry

• Low-dose Active, BID: 8.8% (5/57) versus 3.4% (2/59) on control; risk difference 5.4 percentage points (95% CI -3.3 to 14.1), risk ratio 2.59 (0.52–12.80); unadjusted two-proportion z-test p = 0.224.
• Medium-dose Active, BID: 4.7% (3/64) versus 3.4% (2/59) on control; risk difference 1.3 percentage points (95% CI -5.6 to 8.2), risk ratio 1.38 (0.24–7.99); unadjusted two-proportion z-test p = 0.716.
• High-dose Active, QD: 3.8% (2/52) versus 3.4% (2/59) on control; risk difference 0.5 percentage points (95% CI -6.5 to 7.4), risk ratio 1.13 (0.17–7.77); unadjusted two-proportion z-test p = 0.898.
• High-dose Active, BID: 10.9% (6/55) versus 3.4% (2/59) on control; risk difference 7.5 percentage points (95% CI -1.9 to 17.0), risk ratio 3.22 (0.68–15.28); unadjusted two-proportion z-test p = 0.116.

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.

IGA "Success" - Week 8

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Low-dose Active, BID: 1.9% (1/54) versus 3.6% (2/56) on control; risk difference -1.7 percentage points (95% CI -7.8 to 4.3), risk ratio 0.52 (0.05–5.55); unadjusted two-proportion z-test p = 0.580.
  • Medium-dose Active, BID: 4.8% (3/62) versus 3.6% (2/56) on control; risk difference 1.3 percentage points (95% CI -6.0 to 8.5), risk ratio 1.35 (0.23–7.81); unadjusted two-proportion z-test p = 0.733.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low-dose Active, BID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Medium-dose Active, BID and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary outcomes spanning lesion counts, percent change in lesion counts, and IGA assessments at earlier times or using a related clear/almost-clear definition. Numeric results are posted for Week 8 IGA “success” in two active groups and vehicle, while numerical results for the other listed secondary measures are not reported in the registry record.

Across the posted Week 8 comparisons, the pattern does not establish a consistent advantage for active treatment. The low-dose twice-daily point estimate is below the vehicle estimate, while the medium-dose twice-daily estimate is above it; both intervals include zero. The Week 12 primary outcome has positive point estimates for the active regimens, but its intervals also include zero. The secondary findings therefore do not resolve the uncertainty in the primary comparison or provide a clear, consistent dose pattern.

Secondary outcomes can add context by showing whether related measures or earlier assessments tell a similar story. However, multiple outcomes and assessment times create more opportunities for chance findings. Unless analyses and multiplicity procedures are specified in advance, an isolated secondary result carries less evidential weight than a well-defined primary analysis. The registry record does not report whether these secondary comparisons were prespecified, whether they were adjusted for multiple testing, or how their missing data were handled.

The listed secondary measures should not be treated as interchangeable with the primary endpoint. Lesion counts and percent changes capture different aspects of disease assessment than the combined IGA success criterion. Without the remaining numeric results and the analysis plan, the secondary outcome listing is not enough to establish whether findings were coherent across all measures. It is most appropriate to regard the posted secondary evidence as limited context, not as an independent confirmation of the Week 12 result.

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

• Inflammatory and Non-Inflammatory Lesion Counts - Week 8
• Percent Change in Lesion Counts - Weeks 8 and 12
• IGA "Success" - Week 8
• IGA "Clear" or "Almost Clear" - Weeks 4, 8 and 12

9. Statistical Interpretation

10. Statistical Methods Explained

IGA “success” is a binary endpoint: each participant either satisfies the specified definition or does not. The registry record reports counts of participants meeting the definition and group denominators. A comparison of two such groups can be expressed as a difference in the proportions with success. A positive risk difference means the observed proportion is higher in the active group than in the vehicle group; a negative difference means it is lower. This is a general explanation of risk differences, not a claim about the trial’s prespecified analysis.

The posted pairwise estimates compare each active regimen with the combined vehicle group. For example, the risk difference is reported as 0.054 for low-dose twice daily and 0.075 for high-dose twice daily. The estimates for medium-dose twice daily and high-dose once daily are closer to zero. Because the outcome is uncommon in these groups, relatively few participants determine the estimates. A modest change in the observed number of successes could therefore move the estimated difference noticeably.

A confidence interval describes the range of values compatible with the observed data under the statistical method used, subject to that method’s assumptions. It is not a guarantee that the true effect lies in the interval, and it does not assign a probability to a particular effect after the data are observed. When an interval for a risk difference includes zero, the data are compatible with no difference as well as with differences in either direction. Each posted primary comparison has an interval that includes zero. This is consistent with uncertainty and should not be converted into a conclusion that the groups are equivalent.

The registry record also gives unadjusted p-values for the pairwise comparisons. A p-value measures how unusual data at least as extreme as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The posted values are unadjusted; the record does not report a multiplicity procedure or identify a prespecified inferential threshold for the primary comparisons. Therefore, they should be interpreted alongside the estimates and intervals rather than as standalone verdicts.

The analysis population is per protocol. In the registry description, this means participants from the ITT population who met eligibility criteria, completed the end-of-study visit, and used at least 80% of expected applications. A per-protocol analysis can focus on participants who followed key study requirements, but it may not preserve all the protections of randomized assignment if inclusion depends on events after randomization. The record does not report the detailed participant flow or the reasons participants were excluded from this analysis. It also does not report an ITT estimate for the primary endpoint.

The trial is described as randomized, double-blind, and parallel-group. In general, randomization is intended to make treatment groups comparable at the start, while blinding can reduce some forms of expectation-related influence on assessment or behavior. Those design features do not eliminate uncertainty from small outcome counts, missing assessments, or analytic choices. Details of the randomization method and masking procedures are not reported in the registry record.

General note on over-dispersion: for count outcomes, over-dispersion means the observed variability exceeds what a simple count model assumes. It matters when choosing models and standard errors because an inadequate variance model can make uncertainty appear too small or too large. The primary endpoint is posted as participant counts meeting a binary success definition, not as a rate of repeated events. The registry record does not report an over-dispersion assessment or a model-based analysis for this primary result.

The posted secondary Week 8 IGA comparisons also use binary counts, but they are not a substitute for the primary Week 12 result. Their interpretation is affected by the same small-count and uncertainty issues, as well as by the fact that multiple outcomes and time points are listed. The registry record does not report whether those analyses were prespecified or how multiplicity was addressed. More broadly, it does not report the original statistical analysis plan, model specifications, missing-data methods, interim-analysis methods, or sample-size justification. These omissions limit what can be inferred about the intended confirmatory role of individual comparisons.

The calculations labelled as recalculated, where present, are unadjusted calculations from posted summary statistics; they do not replace a sponsor’s own analysis. No discrepancy is indicated for this record. In general, a recalculation based on summary data cannot reproduce methods that rely on participant-level covariates, stratification, or other details not available in those summaries.

11. Confidence Intervals and Precision

Precision is limited for the Week 12 IGA comparisons. The primary event counts range from 2 to 6 across groups, and the group denominators range from 52 to 64. The confidence intervals for the risk differences all include zero, and their widths allow for materially different possible effects. Thus, the point estimates should not be treated as exact descriptions of the underlying group differences.

For low-dose twice daily, the interval extends from a negative risk difference to a positive one, despite a positive point estimate. The same pattern applies to the other active-versus-vehicle comparisons. The high-dose twice-daily point estimate is the largest positive one, but its interval includes zero as well. The medium-dose twice-daily and high-dose once-daily point estimates are closer to zero, but their intervals also allow a range of effects. These features mean that the posted data do not precisely distinguish the regimens from vehicle.

A confidence interval’s breadth reflects statistical uncertainty under the method used; it does not capture every source of uncertainty. It does not account automatically for selective outcome reporting, unreported analytic choices, or the consequences of restricting the primary analysis to the per-protocol population. Those issues are particularly relevant because the registry record does not report a complete analysis plan or missing-data approach.

The intervals are estimates from the posted group summaries, not proof of equivalence. Demonstrating equivalence or non-inferiority would require an appropriate prespecified margin and analysis, which are not reported in the registry record. The central reading is therefore that the primary comparisons are uncertain, rather than that their effects are precisely zero.

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 original design justification for this trial. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios target 100%, 75%, or 50% of the observed effect. The listed figures are participants per arm for these binary outcomes, not total event counts. The time-to-event exception in the general planning note does not apply to this endpoint.

The 80% power column indicates the illustrative number of participants per arm that would give an 80% chance of detecting the stated effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column represents a higher chance of detecting that same effect, and consequently requires more participants per arm. These are prospective design calculations: they do not tell how likely the observed result was to be detected after the trial has been completed.

For example, planning for 100% of the observed low-dose twice-daily effect gives 309 participants per arm for 80% power and 413 per arm for 90% power. Planning for 75% of that effect gives 492 and 658 per arm, respectively; planning for 50% gives 977 and 1,308. The figures vary substantially by comparison because the observed effects differ and some are close to zero. Smaller effects require more participants to distinguish them from no difference under the stated assumptions.

These calculations use observed effects from a small trial, which can be unstable, especially when event counts are low. The registry record’s own sample-size justification and original design assumptions are not reported. This is not observed power.

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 = 0.034; treatment proportion p₁ = 0.088; average p̄ = 0.061.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3380 = 0.6624.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3358 = 0.2826.
4. n = (0.6624 + 0.2826)² / (0.0538)² = 308.3, rounded up to 309 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 <- 0.0338983050847458                          # control proportion
p1 <- 0.087719298245614                          # 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(1631474)
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 = 309 (80% power), 413 (90% power)
 75% of observed effect: n per arm = 492 (80% power), 658 (90% power)
 50% of observed effect: n per arm = 977 (80% power), 1,308 (90% power)
power.prop.test: 308.3 
Simulated power at n = 309 per arm: 0.822 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The record presents four active-versus-vehicle primary comparisons and lists multiple secondary outcomes and assessment times. When many comparisons are made, the chance of obtaining at least one apparently notable result by chance can increase. Statistical approaches can account for this multiplicity, for example by adjusting significance levels or controlling a family-wise error rate, but the registry record does not report whether any such approach was planned or applied.

The primary comparison p-values are explicitly unadjusted. They should therefore be read as separate comparisons, not as a multiplicity-controlled set of tests. The record does not report a hierarchy among active regimens, a primary contrast selected from the four active regimens, or a rule for interpreting a dose-response pattern. This prevents a confident claim that one regimen is statistically superior to another based on the posted comparisons.

Missing-data handling is also not reported in the registry record. The primary population definition requires end-of-study completion and a minimum level of treatment application, but the record does not give the number or reasons for exclusions from the per-protocol population, or state how missing Week 12 IGA assessments were treated. It does not report a sensitivity analysis for missing outcomes.

The posted primary endpoint is based on a per-protocol subset of the ITT population. The registry record does not provide a corresponding ITT result, nor does it describe whether other analysis populations were used. These gaps matter because the choice of analysis population and assumptions about missing outcomes can affect the estimated group comparison. The original statistical analysis plan, including any planned interim analyses, is not reported in the registry record. Without those details, the posted results cannot establish how closely the reported analysis followed the original plan.

15. 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 2% reporting threshold.

Most frequent non-serious adverse event terms

The safety summary reports serious adverse events, other adverse events, and deaths by group. The serious-adverse-event count is 0 in each group, with the group-specific at-risk counts ranging from 70 to 76. Deaths are also reported as 0 in every group. The record does not list serious adverse-event terms.

For other adverse events, the reported counts are 12 in the low-dose twice-daily group, 18 in the medium-dose twice-daily group, 9 in the high-dose once-daily group, 5 in the high-dose twice-daily group, and 5 in the vehicle group. These are counts of affected participants in the registry safety summary; the record does not provide event descriptions or a statistical comparison in the material.

A zero serious-event count in these groups means no serious events were recorded in the posted summary; it does not establish that the risk is absent. Safety counts are descriptive and should be interpreted with the group denominators and the study’s scope in mind. The registry record does not report detailed event timing, severity grades for other adverse events, or a comparative safety analysis.

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

The posted evidence describes how many participants met a specific IGA success definition at Week 12 in the per-protocol population, and how those counts compared between each active regimen and vehicle. The point estimates for the active-versus-vehicle risk differences are positive, but every reported interval includes zero. That means the data remain compatible with no difference as well as with effects in either direction. The small numbers of successes contribute to broad uncertainty.

The result does not establish that CB-03-01 works or does not work. It also does not establish that the treatment groups are equivalent. Such conclusions would require appropriately designed and reported analyses, including a prespecified margin for equivalence if that were the question. The registry record does not report the full statistical analysis plan, multiplicity approach, or original sample-size justification.

The primary outcome is a particular assessment-based definition: clear or almost clear at Week 12 plus at least a two-grade improvement from baseline. It does not encompass every possible measure of acne, and the posted result is restricted to participants meeting per-protocol requirements. The outcome should not be generalized automatically to all enrolled participants or to other populations, settings, treatment schedules, or durations.

The safety summary records no serious adverse events or deaths in any group, and lists other adverse event counts. Those descriptive data are not enough to establish comparative safety or exclude uncommon harms. Overall, the record offers a description of a randomized Phase 2 study and uncertain estimates for its primary outcome, rather than a definitive conclusion about the relative effects of the regimens.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a point estimate and the precision of that estimate. Some active groups have more observed successes than vehicle, but the intervals remain compatible with no difference. Interpreting only the direction or ordering of the point estimates would overstate what these data establish.

The low event counts also show why binary outcomes can be difficult to estimate precisely in modest-sized groups. A small number of observed successes can produce unstable comparisons, even when the study is randomized and blinded. The design features are valuable, but they cannot remove uncertainty created by sparse outcomes.

The record also highlights the importance of knowing the analysis population. The primary result is per protocol, while the record does not report an ITT result or detailed participant flow. Readers therefore need to distinguish the enrolled sample from the group contributing to the primary endpoint and consider how the eligibility, completion, and adherence requirements may affect interpretation.

Finally, multiple active regimens and secondary outcomes raise questions about multiplicity and prespecification. The registry record does not report how those issues were handled. This limits the strength of any ranking across doses or interpretation of isolated secondary findings. Careful statistical reading keeps the focus on the estimated effects, their uncertainty, and the limits of what the record documents.

18. Limitations

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

The primary endpoint is reported for a per-protocol subset rather than all enrolled participants. Its definition excludes participants who did not meet eligibility criteria, complete the end-of-study visit, or apply at least 80% of expected treatment applications. The registry record does not report detailed reasons for exclusion, participant flow by group, or an ITT analysis of this endpoint.

Success events are few in each group, and the confidence intervals for all posted primary comparisons include zero. This limits precision and makes the observed effects sensitive to small changes in event counts. The group estimates should not be interpreted as a stable dose ranking.

The vehicle arm combines once-daily and twice-daily application schedules. The posted primary comparison therefore does not distinguish outcomes by vehicle schedule. The record also does not report details of the randomization procedure, allocation concealment, or how double blinding was maintained.

Several secondary outcomes and time points are listed, but numeric results are not reported for all of them. Multiplicity adjustment, missing-data methods, and the original statistical analysis plan are not reported in the registry record. These omissions constrain assessment of selective reporting and the role of the posted analyses. The registry record also does not report the original sample-size justification or interim-analysis methods. Safety findings are descriptive, with no reported comparative analysis or detailed adverse-event terms for the other-event counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase 2 Dose Escalating Study to Evaluate the Safety and Efficacy of CB-03-01 Cream in Subjects With Facial Acne Vulgaris — NCT01631474.
• Registry record last updated 2020-11-16; status last verified 2020-10.
• Results first posted 2020-11-16.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01631474 is a completed Phase 2 randomized, double-blind, vehicle-controlled, parallel-group study of CB-03-01 cream for facial acne vulgaris. The record lists enrollment of 363 and describes four active regimens—0.1% twice daily, 0.5% twice daily, and 1% once or twice daily—compared with vehicle applied once or twice daily.

The primary outcome was Week 12 IGA “success,” defined as clear or almost clear and at least a two-grade improvement from baseline. The posted primary counts are low, and all active-versus-vehicle confidence intervals include zero. The analysis population was per protocol. The record also lists secondary outcomes and reports zero serious adverse events and zero deaths in each group.

Detailed statistical plans, missing-data methods, multiplicity handling, and the original sample-size justification are not reported in the registry record. The posted evidence therefore supports a cautious description of uncertain group comparisons, not a definitive ranking of regimens.