A Phase 2b Study to Evaluate RIST4721 in Palmoplantar Pustulosis (PPP): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 2b Study to Evaluate RIST4721 in Palmoplantar Pustulosis (PPP) (NCT05194839), a randomized phase 2 study. The primary outcome is Proportion of Subjects Achieving a 50% Reduction in PPPASI Score.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group Phase 2b dose-ranging study of RIST4721 for palmoplantar pustulosis. It compared two active dose regimens with placebo. Participants assigned to the 400 mg group took 4 active 100 mg tablets once daily for 12 weeks. Those assigned to 200 mg took 2 active 100 mg tablets plus 2 placebo tablets once daily for 12 weeks. The placebo group took 4 placebo tablets once daily for 12 weeks. The registry describes a planned open-label extension after the 12-week blinded phase.

The registry record lists enrollment of 79, a start date of 2022-01-05, and a primary completion date of 2023-02-13. The study status is terminated. The record does not report why it was terminated, and the posted information does not support an inference about the reason or its relationship to the results. A trial being terminated does not, by itself, establish whether the posted endpoint findings are biased or whether the protocol was completed as planned.

The primary endpoint is the number of participants achieving the specified PPPASI reduction between baseline and Week 12. Arm-specific outcome counts are 6 of 12 for RIST4721 400 mg, 3 of 13 for RIST4721 200 mg, and 5 of 12 for placebo. The registry lists two secondary outcomes: absolute change from baseline in PPPGA and absolute change from baseline in PPPASI. Results for those outcomes are not included in the posted figures. Further details about randomization procedures, allocation concealment, and conduct of the extension 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.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Subjects Achieving a 50% Reduction in PPPASI Score, measured over Baseline to Week 12.

The primary endpoint counts participants whose PPPASI score decreased by at least the stated 50% threshold from baseline to Week 12. PPPASI is a measure of palmoplantar disease severity. Its assessment covers the left palm, right palm, left foot, and right foot. At each site, erythema, desquamation (scaling), and pustules are graded for severity, and the affected area is estimated. The site assessments are combined using a formula into a score that can range from 0, meaning absence of disease, to 72, the stated most severe score.

A threshold-based endpoint turns a continuous severity score into a count of participants meeting a defined response criterion. This can make the result straightforward to communicate, but it also means that participants just above and just below the threshold are classified differently despite potentially similar score changes. The endpoint does not show the full distribution of score changes or how far each participant’s change was from the threshold.

In general, such endpoints are useful when a clinically interpretable level of improvement is of interest. Whether the threshold has a particular clinical interpretation for participants in this study is not reported in the registry record. The record also does not provide participant-level PPPASI changes or a detailed description of the statistical analysis used for this endpoint.

7. Results Posted in the Registry

• RIST4721 400 mg: 50.0% (6/12) versus 41.7% (5/12) on control; risk difference 8.3 percentage points (95% CI -31.4 to 48.1), risk ratio 1.20 (0.50–2.88); unadjusted two-proportion z-test p = 0.682.
• RIST4721 200 mg: 23.1% (3/13) versus 41.7% (5/12) on control; risk difference -18.6 percentage points (95% CI -54.7 to 17.5), risk ratio 0.55 (0.17–1.83); unadjusted two-proportion z-test p = 0.319.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a risk difference describe?

The primary endpoint is binary at the participant level: each participant either meets the PPPASI response threshold or does not. A risk difference expresses the difference between the proportions meeting that threshold in two groups. In the posted comparisons, the estimate is expressed as the RIST4721 group minus placebo. A positive estimate therefore points toward a larger response proportion in the active group; a negative estimate points toward a smaller response proportion. This direction describes the estimate, not proof of a causal effect.

For RIST4721 400 mg versus placebo, the risk difference is 0.083. For RIST4721 200 mg versus placebo, it is -0.186. These estimates are derived from small arm-specific counts: 6 of 12 and 5 of 12 for the 400 mg comparison, and 3 of 13 and 5 of 12 for the 200 mg comparison. With relatively few participants contributing to each comparison, moving only a small number of outcomes can meaningfully change the observed proportions and the estimated difference.

How do confidence intervals help?

A confidence interval gives a range of estimates compatible with the observed data under the method used to calculate it. It communicates precision as well as direction. An interval that is narrow represents a more precise estimate than a broad interval, while an interval that crosses zero for a risk difference includes no difference as one compatible possibility. In general, the interval is not a guarantee that the true value lies within its limits, and it does not show the probability that a particular value is true.

The posted intervals for both risk differences include zero and extend to values in both directions. They are broad, indicating that the small groups leave considerable uncertainty about the size of the difference. The p-values are unadjusted: 0.682 for the 400 mg comparison and 0.319 for the 200 mg comparison. A p-value summarizes how unusual data at least as discrepant as those observed would be under a specified null model and analysis. It does not measure the probability that the treatment has no effect, nor does it measure clinical importance.

What do the relative measures add?

The risk ratio compares response proportions as a ratio, while the odds ratio compares response odds. Each offers a different scale for describing the same binary outcome. In general, estimates near 1 correspond to similar groups on that relative scale; values above or below 1 indicate direction of the contrast. Interpretation still depends on the uncertainty interval and the underlying event counts. Here, both the risk-ratio and odds-ratio intervals are wide for each comparison, so the relative estimates do not resolve the uncertainty seen in the risk differences.

These measures are not interchangeable. A risk difference describes an absolute contrast, whereas ratios describe a relative contrast. When response is not rare, the odds ratio can be farther from 1 than the risk ratio for a similar underlying pattern. The posted estimates should therefore be interpreted on their stated scales rather than translated into a newly calculated measure.

What does the design contribute?

Randomization is intended, in general, to make assigned groups comparable at the start of a trial with respect to measured and unmeasured characteristics, on average. Double blinding is intended to limit the influence of treatment knowledge on participant behavior, care, or outcome assessment. A parallel design assigns participants to a group and compares those groups over the treatment period. These design labels describe the stated study structure; the registry record does not report enough procedural detail to assess how randomization and masking were implemented.

The primary outcome is assessed from baseline to Week 12. Using a defined threshold makes the endpoint a responder count, but it discards information about the magnitude of changes on either side of the threshold. The registry record does not report a model, covariate adjustment, confidence-interval method, or other analytic details for the primary endpoint. The posted statistics can be described, but the exact underlying analysis choices cannot be verified from the registry record.

What are the planning calculations?

The sample-size illustrations use the observed effect as their starting point and consider stated fractions of that effect. Their assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The planning calculations are not the original trial design justification; those original assumptions are not reported in the registry record. The illustrations indicate the number of participants per arm needed under their stated assumptions, rather than the number actually analyzed. They should not be treated as a retrospective measure of the trial’s ability to detect an effect.

In general, estimates from small groups are more sensitive to random variation, and a sample-size calculation based on the observed effect can be unstable when that estimate is imprecise. The calculations are best read as conditional planning illustrations, not as independent evidence that the observed differences are real or reproducible.

10. Confidence Intervals and Precision

The risk-difference confidence intervals are broad relative to the estimates. For RIST4721 400 mg versus placebo, the estimate is 0.083 and its 95% confidence interval runs from -0.314 to 0.481. For RIST4721 200 mg versus placebo, the estimate is -0.186 and its 95% confidence interval runs from -0.547 to 0.175. Each interval includes zero and extends to potentially meaningful differences in either direction. The posted data therefore do not pin down the direction or magnitude of either comparison with precision.

In general, a confidence interval describes sampling uncertainty under the analysis method used. It is not a range containing every plausible source of uncertainty: it does not automatically account for missing data, departures from the planned analysis, bias, or multiple comparisons. Those issues require information about conduct and analysis that is not fully reported in the registry record.

The relative-effect intervals are also wide. For the 400 mg comparison, the risk ratio is 1.2 with a 95% confidence interval from 0.499 to 2.883, and the odds ratio is 1.4 with a 95% confidence interval from 0.279 to 7.016. For the 200 mg comparison, the risk ratio is 0.554 with a 95% confidence interval from 0.167 to 1.834, and the odds ratio is 0.42 with a 95% confidence interval from 0.075 to 2.361. These intervals likewise include a broad range of possible relative differences.

Small group counts contribute to imprecision because each observed response carries substantial weight in the group estimate. The posted intervals are more informative about uncertainty than a simple comparison of response counts alone. They do not establish equivalence, and they do not identify a reliably superior dose.

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 figures are planning illustrations, not observed trial results. For these binary endpoint comparisons, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculation starts from the observed effect and considers 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The original trial’s own sample-size assumptions and design justification are not reported in the registry record.

The 80% power column gives the planned participants per arm under the stated assumptions for an analysis with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses the same concept with a higher target chance of detection. These are conditional planning quantities, not guarantees about what a future trial will find. They depend on the effect size and assumptions used in the calculation.

For the 400 mg comparison, the listed participants per arm for 80% power are 561 when planning for 100% of the observed effect, 993 for 75%, and 2,224 for 50%. The corresponding 90% power figures are 750, 1,329, and 2,977. For the 200 mg comparison, the listed 80% figures are 99, 182, and 423, while the 90% figures are 132, 243, and 566. Smaller effects require more participants under these planning assumptions. These figures are not observed power: they do not describe the probability that this completed trial detected an effect.

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 = 0.417; treatment proportion p₁ = 0.500; average p̄ = 0.458.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7046 = 1.3811.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7022 = 0.5910.
4. n = (1.3811 + 0.5910)² / (0.0833)² = 560.0, rounded up to 561 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 <- 0.416666666666667                          # control proportion
p1 <- 0.5                          # 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(5194839)
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 = 561 (80% power), 750 (90% power)
 75% of observed effect: n per arm = 993 (80% power), 1,329 (90% power)
 50% of observed effect: n per arm = 2,224 (80% power), 2,977 (90% power)
power.prop.test: 560 
Simulated power at n = 561 per arm: 0.807 (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 one primary outcome and two secondary outcomes: absolute change from baseline in PPPGA and absolute change from baseline in PPPASI. The posted primary results include two active-dose comparisons with placebo. When multiple outcomes or comparisons are considered, the chance of at least one apparently unusual result can increase if no adjustment or prespecified testing strategy is used. In general, multiplicity procedures can control that issue, but the registry record does not report whether a strategy was planned or applied. The posted p-values are unadjusted, so they should not be interpreted as multiplicity-adjusted evidence.

The record lists zero analyses. It does not provide a detailed statistical analysis plan, explain whether the two dose comparisons were formally tested, or state whether subgroup or interim analyses were conducted. Those details are not reported in the registry record. No conclusion should be drawn from their absence about what analyses were or were not performed outside the posted entries.

Handling of missing primary outcome data is also not reported in the registry record. The primary outcome lists 12 participants for RIST4721 400 mg, 13 for RIST4721 200 mg, and 12 for placebo, while overall enrollment is 79. The safety summaries list different group sizes. The record does not explain how the endpoint analysis populations were defined, whether any participants lacked endpoint data, or how missingness was handled. This prevents a full assessment of whether the posted comparisons reflect all randomized participants.

Information about the intention-to-treat population, per-protocol analyses, protocol deviations, and exclusions is not reported in the registry record. These details matter because excluding participants or analyzing only a subset can affect the interpretation of a randomized comparison. Without them, the posted counts should be understood as the registry’s reported endpoint results, with the analysis population and missing-data procedures unresolved.

14. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hepatic lesion (3.8%), blood bilirubin increased (3.8%).

The safety summary reports serious adverse events for each group using a group-specific number at risk and number affected. In the RIST4721 400 mg group, 0 of 27 were affected; in the RIST4721 200 mg group, 1 of 26 was affected; and in the placebo group, 0 of 26 was affected. The record reports no deaths in any group. These are counts from the posted safety summary and are separate from the primary efficacy endpoint counts.

The listed top serious-event terms are hepatic lesion and blood bilirubin increased, each reported as 3.8%. The registry summary does not specify the group associated with each term in this listing. Serious-event summaries based on few events cannot establish whether a difference between groups is meaningful, and the absence of a reported event in a group does not establish that the risk is zero.

In general, safety counts describe events reported during the recorded observation period; they do not by themselves establish that a study treatment caused an event. The registry record does not provide enough detail to assess event timing, relatedness judgments, exposure-adjusted rates, or the complete non-serious adverse-event profile.

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

The posted primary data describe the number of participants meeting a defined PPPASI response threshold by Week 12. There were 6 responders among 12 participants in the RIST4721 400 mg group, 3 among 13 in the RIST4721 200 mg group, and 5 among 12 in the placebo group. The associated risk-difference estimates are imprecise, and both confidence intervals include zero. The results therefore do not determine a clear direction or precise size for either dose comparison.

These findings do not prove that RIST4721 is effective or ineffective. A non-significant unadjusted p-value is not proof of no effect, while an observed difference in counts is not proof of a treatment effect. The uncertainty intervals include a range of values, and the small outcome groups leave limited precision. The comparisons also do not establish that one active dose is better than the other.

The endpoint captures whether a participant crossed a threshold, not the full pattern of change in PPPASI score. The posted results do not show how much scores changed for individual participants or how close non-responders were to the response threshold. Although the registry lists PPPGA and absolute PPPASI change as secondary outcomes, results for those outcomes are not included in the posted findings.

The trial’s terminated status is part of the record, but the reason is not reported in the registry record. It would be speculative to connect termination to efficacy, safety, recruitment, or another cause. Likewise, the registry does not report enough information about missing data or analysis populations to determine how the primary outcome counts relate to all enrolled participants.

The most defensible interpretation is limited: the posted counts and estimates are descriptive results from a randomized, blinded, placebo-controlled study, with substantial uncertainty around the comparisons. They do not settle the treatment question, and they should not be used as medical advice or as a substitute for evidence from the broader clinical research record.

16. Why This Trial Matters Statistically

This trial is statistically informative as an example of how a randomized design can still produce uncertain estimates when the endpoint groups are small. The posted responder counts are close for the RIST4721 400 mg and placebo groups, while the RIST4721 200 mg count is lower than the placebo count. Neither pattern alone is enough to establish a difference. The confidence intervals make the uncertainty visible and discourage overinterpretation of the raw counts.

The study also illustrates the importance of separating statistical significance from estimation. The unadjusted p-values do not summarize the likely size of a difference, and they do not show whether a clinically important difference can be ruled out. The confidence intervals are broad enough that substantially different underlying effects remain compatible with the data. Reporting estimates with uncertainty is therefore more informative than treating a p-value as a verdict.

The dose-ranging structure raises an additional design question: how should multiple active-dose comparisons be interpreted? The registry record posts estimates for two comparisons, but does not report a multiplicity strategy or detailed analysis plan. This leaves uncertainty about the inferential role of the separate tests. The sample-size illustrations also show how planning results depend on which fraction of an observed, uncertain effect is targeted.

Finally, the record’s enrollment, outcome-analysis counts, safety groups, and terminated status require careful reading rather than assumptions. The reason for the differences in reported group counts and the reason for termination are not reported in the registry record. A statistically responsible interpretation distinguishes what the record states from what it leaves unresolved.

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.

The primary endpoint results are based on small arm-specific groups, and the risk-difference confidence intervals are broad. This limits precision and makes estimates sensitive to a small number of outcome classifications. The threshold endpoint also omits information about the magnitude of PPPASI change for participants who did not meet the response criterion.

The registry record does not report the original sample-size justification, detailed analysis plan, confidence-interval method, randomization procedures, or allocation-concealment methods. The posted planning calculations are based on the observed effects and should not be mistaken for the trial’s original design rationale. The registry does not report whether multiplicity was addressed, whether interim analyses occurred, or whether the posted comparisons were prespecified.

Overall enrollment is 79, but the primary outcome counts are reported for groups of 12, 13, and 12 participants, while the safety groups have their own at-risk counts. Reasons for these differences, endpoint missingness, analysis-population definitions, and missing-data methods are not reported in the registry record. The record also does not explain why the trial was terminated or provide results for its listed secondary outcomes.

These limitations do not show that the results are biased, but they constrain how fully the results can be assessed. The estimates should be interpreted as the posted registry findings, with uncertainty about both precision and some aspects of analysis and trial conduct.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Phase 2b Study to Evaluate RIST4721 in Palmoplantar Pustulosis (PPP) — NCT05194839.
• Registry record last updated 2023-06-29; status last verified 2023-06.
• Results first posted 2023-06-29.
• 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

The registry describes a randomized, double-blind, placebo-controlled, parallel-group Phase 2b study of RIST4721 in palmoplantar pustulosis. The study compared once-daily 400 mg and 200 mg regimens with placebo over 12 weeks, followed by a planned open-label extension. Enrollment was 79; the study is listed as terminated, with primary completion on 2023-02-13.

The primary endpoint was the number of participants achieving a 50% reduction in PPPASI score from baseline to Week 12. Posted counts were 6 of 12 for RIST4721 400 mg, 3 of 13 for RIST4721 200 mg, and 5 of 12 for placebo. Both dose comparisons have broad risk-difference confidence intervals that include zero. Reasons for termination, missing-data handling, and the original sample-size justification are not reported in the registry record.