KD025 in Subjects With Diffuse Cutaneous Systemic Sclerosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for KD025 in Subjects With Diffuse Cutaneous Systemic Sclerosis (NCT03919799), a randomized phase 2 study. The primary outcome is DB Period: Number of Participants With Combined Response Index in Diffuse Cutaneous Systemic Sclerosis (CRISS) Score Greater Than or Equal to (>=) 60 Percent (%) at Week 24.

2. Clinical Question

The clinical question was whether participants receiving either of two belumosudil dosing schedules were more likely than participants receiving placebo to meet the trial’s definition of improvement at Week 24. The primary outcome classified participants according to whether their Combined Response Index in Diffuse Cutaneous Systemic Sclerosis (CRISS) score reached the stated threshold. CRISS draws on several domains, including skin involvement, lung function, clinician and participant assessments, and disability.

The registry describes a randomized comparison across three groups, with the two active-dose groups assessed separately against placebo. The endpoint is a binary classification based on a score threshold, rather than the average change in CRISS score. Thus, the primary comparison addresses the frequency of participants who crossed the specified response threshold; it does not describe every change in the underlying CRISS domains or score.

3. Trial Design

The registry describes a phase 2, randomized, placebo-controlled, parallel-group, multicenter study of belumosudil, also called KD025, in diffuse cutaneous systemic sclerosis. It records quadruple masking. The study summary describes the initial period as double-blind; the registry record does not explain how the masking labels correspond to the study procedures.

During the initial double-blind period, participants were assigned in a 1:1:1 ratio to belumosudil 200 mg once daily, belumosudil 200 mg twice daily, or matched placebo. Dosing in this period lasted 28 weeks. Participants assigned to either belumosudil schedule continued on the same schedule during the open-label extension. After unblinding, participants who had received placebo were re-randomized to one of the two belumosudil schedules for the extension. The planned treatment duration was 52 weeks, with the extension lasting 24 weeks.

The registry reports enrollment of 36 participants and says enrollment was terminated earlier than planned for business reasons unrelated to safety. The original enrollment target and the statistical rationale for that target are not reported in the registry record. The record gives a study start date of 2019-06-26 and a primary completion date of 2022-08-09, and lists the status as terminated.

The primary endpoint discussed in this analysis belongs to the double-blind period and was assessed at Week 24. The trial also listed outcomes in the open-label extension and other clinical and laboratory measures. The registry record does not report the protocol’s full statistical analysis plan, whether interim analyses were planned, or detailed procedures for maintaining masking.

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: A total of 36 participants were enrolled and randomized into 3 groups in 1:1:1 ratio in double blind (DB) period of this study. The study was DB for first 28 weeks followed by an open-label extension (OLE) period of 24 weeks. After unblinding (i.e., in OLE), the participants who received belumosudil in DB period continued on same belumosudil dose whereas participants who received placebo were re-randomized in OLE period to one of the belumosudil doses (200 mg QD or 200 mg BID) in a 1:1 ratio.

DB Period (28 Weeks)

Reasons for not completing this period:

OLE Period (24 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on mITT population.

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: Analysis was performed on modified intent-to-treat (mITT) population which included all participants who received at least one dose of the study drug.

6. Primary Endpoint

The registry lists the primary outcome as DB Period: Number of Participants With Combined Response Index in Diffuse Cutaneous Systemic Sclerosis (CRISS) Score Greater Than or Equal to (>=) 60 Percent (%) at Week 24, measured over Week 24.

The primary endpoint counted participants whose CRISS score was at least 60 percent at Week 24. CRISS combines information from modified Rodnan skin score (mRSS), percent predicted forced vital capacity (FVC), physician and participant global assessments, and the Scleroderma Health Assessment Questionnaire-Disability Index. Its algorithm estimates the probability of improvement from baseline using changes across these domains. The score ranges from 0.0 to 1.0, with higher scores indicating a greater predicted probability of improvement.

The registry describes 60 percent as the minimally important difference threshold for this binary endpoint. Converting the score into a responder classification gives a clinically interpretable count: how many participants met the chosen response criterion in each group. However, it discards detail about how far a participant’s score was from the threshold, and participants just below and just above it are placed in different categories.

The endpoint also applies a specific rule for certain worsening events. Participants developing new onset of renal crisis, new onset or worsening of lung fibrosis, new onset of pulmonary arterial hypertension, or new onset of left ventricular failure were assigned a probability of improvement equal to 0.0. Missing data were handled using last observation carried forward. The registry record does not provide further detail on the timing or implementation of that method.

CRISS was used to combine changes across several disease-related domains rather than relying on a single measure. Its binary threshold therefore represents a particular summary of those domains, not a complete account of each domain’s course.

7. Results Posted in the Registry

• DB Period: Belumosudil QD: 54.5% (6/11) versus 58.3% (7/12) on control; risk difference -3.8 percentage points (95% CI -44.3 to 36.8), risk ratio 0.94 (0.45–1.92); unadjusted two-proportion z-test p = 0.855.
• DB Period: Belumosudil BID: 25.0% (3/12) versus 58.3% (7/12) on control; risk difference -33.3 percentage points (95% CI -70.5 to 3.8), risk ratio 0.43 (0.14–1.28); unadjusted two-proportion z-test p = 0.098.

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.

DB Period: Change From Baseline in 12-lead Electrocardiogram (ECG) Values: Heart Rate at Week 24

• 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:
  • DB Period: Belumosudil QD: mean -3.60 versus -5.50 on control; difference 1.90 (95% CI -6.33 to 10.13), standardized effect d = 0.20; z-test p = 0.651.
  • DB Period: Belumosudil BID: mean -2.10 versus -5.50 on control; difference 3.40 (95% CI -3.20 to 10.00), standardized effect d = 0.42; z-test p = 0.313.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB Period: Belumosudil QD 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 DB Period: Belumosudil BID and the control. The interval gives the range of effects that remain compatible with the data.

DB Period: Change From Baseline in Hematological Parameter: Hematocrit at Week 24

• 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:
  • DB Period: Belumosudil QD: mean 0.00 versus 0.01 on control; difference -0.01 (95% CI -0.05 to 0.03), standardized effect d = -0.19; z-test p = 0.648.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB Period: Belumosudil QD and the control. The interval gives the range of effects that remain compatible with the data.

DB Period: Change From Baseline in Hematological Parameter: Hemoglobin at Week 24

• 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:
  • DB Period: Belumosudil QD: mean 1.20 versus 2.60 on control; difference -1.40 (95% CI -14.05 to 11.25), standardized effect d = -0.09; z-test p = 0.828.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB Period: Belumosudil QD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 70 secondary outcome measures, covering additional CRISS assessments, skin score, lung function, global assessments, disability, and other measures. The posted numerical summaries included for this analysis illustrate a range of changes rather than a uniformly aligned pattern across the secondary outcomes. Because these summaries cover only selected measures, they cannot support a complete account of the results across all listed secondary outcomes.

Secondary outcomes provide context for the primary endpoint by examining other aspects of health or different ways of measuring change. They may help show whether the primary result is consistent with observations in related domains, but they do not replace the prespecified primary comparison. The primary endpoint is a thresholded composite at Week 24, whereas the secondary measures can use continuous change scores or different time points. Differences in scale and timing mean results do not necessarily have to move in the same direction.

Unadjusted secondary comparisons carry less evidential weight when many outcomes are examined. As a general statistical matter, testing multiple outcomes increases the chance that some results may appear unusual through random variation alone. The registry record does not report a multiplicity-control strategy for the secondary outcomes, so isolated nominal findings should be treated as exploratory rather than as independent confirmation of the primary result.

Detailed numerical results and analysis methods are not available in the record for every listed secondary outcome in the material summarized. The broader secondary pattern and its relationship to the primary endpoint therefore cannot be determined fully from the registry record. The listed measures can inform context, but they do not resolve the primary endpoint’s imprecision.

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

• DB Period: Combined Response Index in Diffuse Cutaneous Systemic Sclerosis Score at Week 24
• OLE Period: Combined Response Index in Diffuse Cutaneous Systemic Sclerosis Score at Week 52
• DB Period: Change From Baseline in Modified Rodnan Skin Score (mRSS) at Week 24
• DB Period: Change From Baseline in Percent Predicted Forced Vital Capacity (FVC) at Week 24
• DB Period: Change From Baseline in Physician Global Assessment of Participant's Overall Health Using Visual Analogue Scale Score at Week 24
• DB Period: Change From Baseline in Patient Global Assessment of Participant's Overall Health Using Visual Analogue Scale Score at Week 24
• DB Period: Change From Baseline in Scleroderma Health Assessment Questionnaire-Disability Index (SHAQ-DI) Total Score at Week 24
• DB Period: Percentage Improvement in Modified Rodnan Skin Score at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome: each participant is classified as meeting or not meeting the CRISS threshold. For each group, the observed count and group size describe the response frequency. A comparison can then be expressed on different scales, including an odds ratio or a risk difference. These measures answer related but distinct questions, so their numerical values should not be treated as interchangeable.

What does the risk difference describe?

The risk difference subtracts the response proportion in placebo from the response proportion in an active-dose group. A value below zero means the observed response proportion was lower in that active group; a value above zero means it was higher. The recalculated differences use the posted counts without adjustment for other variables. They are not the same estimator as the sponsor’s logistic-regression odds ratios.

The simple recalculation gives a risk difference of -0.038 for once-daily dosing compared with placebo and -0.333 for twice-daily dosing compared with placebo. The corresponding intervals are -0.443 to 0.368 and -0.705 to 0.038. These intervals include zero, which represents no difference on the risk-difference scale. Their width also conveys that the data are compatible with a range of potentially meaningful differences in either direction.

Why use logistic regression?

Logistic regression models the odds of a binary outcome. The registry reports odds ratios from logistic regression for each active-dose comparison with placebo. An odds ratio of 1 represents equal odds in the groups; values on either side indicate different estimated odds. The reported intervals extend across 1 for both comparisons, indicating that the estimates are imprecise and do not distinguish clearly from equal odds. The registry record does not report enough model detail to identify all covariates or other adjustments, so the regression should be described only as the reported logistic-regression analysis.

Odds ratios and risk differences present results on different scales. The odds ratio compares odds, while the risk difference compares proportions directly. When response proportions are not rare, the odds ratio should not be read as if it were a relative probability. The registry’s model-based odds ratios and the unadjusted risk differences can therefore differ in numerical form without representing contradictory calculations. The registry record does not provide a direct conversion between these measures.

What does a confidence interval communicate?

A confidence interval expresses the uncertainty around an estimate under the statistical method used. A broad interval indicates limited precision: the observed data do not pin down the effect closely. For the primary comparisons, the intervals include both no difference and values in either direction. This is why the point estimate alone should not be read as a definitive account of the treatment contrast. The interval is not a range containing a known share of individual participant outcomes, and it does not give the probability that the true effect lies inside its endpoints.

How should p-values be read?

A p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The unadjusted p-values accompanying the simple recalculations are separate from the sponsor’s reported regression p-values. Since they arise from different analyses, they need not match. Neither p-value establishes equivalence, and interpretation should account for the estimates, intervals, endpoint definition, small group counts, and other analyses in the trial.

What does the analysis population mean?

The registry states that the primary endpoint analysis was performed in the modified intention-to-treat population. The record does not define the exact inclusion rules for that population or explain how exclusions were handled. The arm counts associated with the endpoint are the denominators for the posted outcome results; enrollment is a separate trial-level figure and should not be substituted for those endpoint denominators.

How do missing outcomes affect interpretation?

The endpoint description states that last observation carried forward was used for missing data. This approach uses a participant’s last recorded value in place of a later missing value. As a general statistical matter, it can make the result depend on assumptions about how the outcome would have evolved after the last observation. The registry record does not report the amount or pattern of missingness, sensitivity analyses, or whether alternative missing-data approaches were used. The impact of missing data on the primary estimate therefore cannot be assessed from the registry record.

11. Confidence Intervals and Precision

Precision is limited for the primary comparisons. For once-daily belumosudil versus placebo, the recalculated risk difference is -0.038 and its 95% confidence interval ranges from -0.443 to 0.368. For twice-daily belumosudil versus placebo, the recalculated difference is -0.333 and its 95% interval ranges from -0.705 to 0.038. Each interval includes zero, as well as values on both sides of zero. Thus, the observed counts do not narrowly locate the difference between groups.

The reported logistic-regression intervals also extend broadly: 0.19 to 5.82 for the once-daily comparison and 0.07 to 2.35 for the twice-daily comparison. On the odds-ratio scale, these intervals include 1, the value corresponding to equal odds. The range of compatible values is wide, so the point estimates should not be treated as precise estimates of the underlying contrast.

Wide intervals are expected to be a concern when group counts are small and the outcome is binary: a small change in the number of participants classified as responders can materially change the estimated group contrast. The primary endpoint also reduces a continuous score to a threshold classification, which can leave less information in the analysis than the underlying score contains.

A confidence interval describes uncertainty under its method and assumptions; it does not measure the range of participant outcomes or prove that every value in the interval is equally plausible. Nor does an interval crossing the null establish that the groups are equivalent. The original study’s planned precision target and sample-size justification are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not a report of the trial’s original design. For these binary comparisons, the figures are participants per arm. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The original protocol’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column describes the corresponding planning target for a 90% chance. These are design illustrations for hypothetical future comparisons, not descriptions of what happened in this trial.

Each planning row scales the effect to be detected relative to the observed effect. Planning for a smaller effect requires more participants, because a smaller difference is harder to distinguish from random variation. Estimates based on the observed effect can be especially unstable when the trial groups are small, so these figures should not be interpreted as reliable forecasts without considering other design information. The registry record does not report the trial’s original target enrollment or its original power calculation.

This is not observed power. It is a planning illustration computed from the observed effect under stated assumptions, not a retrospective measure of the trial’s ability to answer its question. The power figures do not change the interpretation of the confidence intervals or resolve the uncertainty in the posted results.

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 = 0.583; treatment proportion p₁ = 0.545; average p̄ = 0.564.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7012 = 1.3744.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7007 = 0.5897.
4. n = (1.3744 + 0.5897)² / (-0.0379)² = 2,688.6, rounded up to 2,689 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 <- 0.583333333333333                          # control proportion
p1 <- 0.545454545454545                          # 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(3919799)
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 = 2,689 (80% power), 3,599 (90% power)
 75% of observed effect: n per arm = 4,769 (80% power), 6,384 (90% power)
 50% of observed effect: n per arm = 10,701 (80% power), 14,325 (90% power)
power.prop.test: 2688.6 
Simulated power at n = 2,689 per arm: 0.796 (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’s own primary analyses are logistic-regression comparisons reported as odds ratios. For once-daily belumosudil versus placebo, the reported odds ratio is 1.06, with a 95% confidence interval from 0.19 to 5.82 and p = 0.947. For twice-daily belumosudil versus placebo, it is 0.39, with a 95% confidence interval from 0.07 to 2.35 and p = 0.308. The registry record labels both as superiority analyses.

The recalculated figures use the posted response counts to estimate unadjusted risk differences and p-values. They are a transparent, simple comparison of the observed group proportions, but they do not reproduce the sponsor’s logistic-regression model. Odds ratios and risk differences use different scales, and the model details beyond logistic regression are not reported in the registry record. The two sets of estimates should therefore be presented as different analyses rather than treated as interchangeable checks of exactly the same calculation.

The reported sponsor analyses are the registry’s formal analyses for the primary endpoint. The simple recalculations can help readers understand the event counts and direct group differences, but do not replace those analyses. Both the sponsor-reported intervals and the recalculated intervals indicate substantial uncertainty; neither analysis establishes a clear difference from placebo.

15. Multiplicity, Missing Data and Analysis Populations

The trial compared two active-dose groups with a common placebo group for the primary endpoint and also listed many secondary outcomes. When several hypotheses are tested, the chance of at least one apparently notable result arising by chance can increase. Statistical approaches that account for multiple testing can help control this issue. The registry record does not report whether a multiplicity strategy was specified for the primary comparisons, secondary outcomes, or both. The unadjusted recalculated p-values should therefore be understood as unadjusted comparisons, not as evidence that a family of tests has been controlled.

The registry reports logistic regression for the primary comparisons, but the full model specification and analysis plan are not reported in the registry record. It is not reported whether analyses were prespecified in a protocol or statistical analysis plan, whether interim analyses were conducted, or what rules governed any such analyses. Those omissions limit the ability to assess how the reported analyses relate to the complete planned testing strategy.

The primary analysis used a modified intention-to-treat population. The registry record does not define the membership rules for that population, report reasons for any exclusions, or provide a participant flow account sufficient to assess the difference between enrollment and analysis populations. It also states that last observation carried forward was used for missing primary endpoint data, but the extent and pattern of missingness and the results of sensitivity analyses are not reported in the registry record.

As a general statistical matter, missing-data methods depend on assumptions about the unobserved outcomes. Carrying the last observed value forward may not reflect later change, particularly if missingness is related to health status or treatment experience. Without information about missingness or alternative analyses, the robustness of the endpoint result to those assumptions cannot be evaluated. These limitations do not establish that the estimates are biased, but they restrict what can be concluded about their reliability.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac failure congestive (10.0%), pneumonia aspiration (10.0%), covid-19 (9.1%), flank pain (9.1%), anaemia (8.3%).

During the double-blind period, the registry reports serious adverse events affecting 2 participants in the once-daily group, 0 in the twice-daily group, and 3 in the placebo group. It reports other adverse events affecting 10, 11, and 11 participants in those respective groups. No deaths are reported in the listed groups. These counts describe the registry’s posted safety outcomes; they are not a comparison adjusted for differences in follow-up or other factors.

The open-label extension lists separate groups, including participants continuing belumosudil and participants who had received placebo before re-randomization. Serious adverse events were reported for 0 participants in the extension once-daily group, 0 in the placebo-to-once-daily group, 1 in the extension twice-daily group, and 0 in the placebo-to-twice-daily group. The extension is not a continued blinded placebo comparison, so its counts should not be read as a randomized comparison with an unchanged placebo group.

The registry also lists serious adverse event terms with percentages, including congestive cardiac failure and aspiration pneumonia at 10.0% each. The record does not provide a basis in these figures for assigning those terms to a particular treatment group. Small group counts and differing study periods limit comparisons. Safety counts alone do not establish causation or quantify the risk beyond the trial record.

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

The primary results describe how many participants in each double-blind group met the CRISS response threshold at Week 24 and how uncertain the estimated comparisons are. The observed counts and the registry’s logistic-regression results do not establish a clear difference between either belumosudil dose and placebo. The broad confidence intervals leave substantial uncertainty about the magnitude and direction of the underlying contrasts.

These findings do not demonstrate that the treatments are equivalent. A failure to distinguish a group from placebo is not the same as evidence that their effects are identical; equivalence requires a design and analysis that specify an acceptable range of differences. Nor should the posted results be summarized as proof that either dose works or does not work. They are estimates from a small phase 2 study that was terminated earlier than planned, with enrollment stopped for business reasons unrelated to safety.

The primary outcome has a specific meaning: meeting a threshold on an algorithmic composite of several domains. It does not show which domain drove a participant’s classification, how all participants’ continuous scores changed, or whether every aspect of disease status moved in the same direction. The use of last observation carried forward for missing data adds assumptions that cannot be evaluated fully because missingness details and sensitivity analyses are not reported in the registry record.

The open-label extension addressed later treatment exposure but does not preserve the original placebo comparison: participants previously assigned placebo were re-randomized to active dosing after unblinding. The Week 24 primary result should therefore remain distinct from extension outcomes and from safety counts. Overall, the registry supports a description of observed responses and their uncertainty, not a definitive causal or clinical conclusion.

18. Why This Trial Matters Statistically

This study illustrates why clinical-trial interpretation depends on more than the direction of a point estimate. The observed response counts differ across groups, but the group sizes are small and the uncertainty intervals are broad. Readers need to consider the estimate, its interval, the analysis method, and the endpoint definition together rather than treating one count or p-value as a verdict.

It also demonstrates the importance of distinguishing effect measures. The sponsor’s logistic-regression odds ratios and the unadjusted risk differences describe the same posted endpoint on different scales and arise from different analyses. Making that distinction explicit prevents an odds ratio from being mistaken for a direct difference in response proportions and helps readers understand why separate estimates need not match numerically.

The primary outcome is a composite converted into a threshold-based responder classification. Such an endpoint can be useful for summarizing several disease-related domains, but its interpretation depends on the algorithm, threshold, and rules for worsening events and missing data. Those choices shape what counts as improvement and what information is lost when a score becomes a binary outcome.

Finally, early termination and an unreported original sample-size rationale matter to interpretation without explaining the results by themselves. The registry states that termination was for business reasons unrelated to safety, but the reason does not eliminate uncertainty about the observed comparisons. This record is a useful example of how to separate reported findings, simple recalculations, design information, and unanswered questions.

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.

The primary analysis is based on limited group counts, and its confidence intervals are broad. This leaves the effect estimate imprecise. The study was terminated earlier than planned for business reasons unrelated to safety, but the registry record does not state the original enrollment target, quantify how termination affected the planned analysis, or provide the original statistical rationale.

The primary endpoint is a thresholded composite. It compresses changes across mRSS, FVC percent predicted, physician and participant global assessments, and SHAQ-DI into a responder classification. That classification does not show the separate contributions of each domain. It also uses a rule assigning a score of 0.0 for specified new or worsening events, and missing data were handled with last observation carried forward. The extent of missingness and sensitivity analyses are not reported in the registry record.

The registry reports logistic regression but does not provide the full model specification in the available record. It also does not report a detailed multiplicity strategy, the complete statistical analysis plan, or whether interim analyses occurred. These gaps make it difficult to assess the prespecification and robustness of the full set of comparisons.

The open-label extension followed unblinding, and former placebo participants were re-randomized to active dosing. Extension outcomes therefore do not retain the original placebo contrast. The record’s quadruple-masking label and description of a double-blind period are both reported, but their relationship is not explained. These features, along with the small study and early termination, mean results should be interpreted as limited estimates rather than definitive evidence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: KD025 in Subjects With Diffuse Cutaneous Systemic Sclerosis — NCT03919799.
• Registry record last updated 2023-08-30; status last verified 2023-08.
• Results first posted 2023-08-30.
• 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

NCT03919799 is a randomized, phase 2, placebo-controlled study of belumosudil in diffuse cutaneous systemic sclerosis. The registry reports enrollment of 36 participants and early termination for business reasons unrelated to safety. In the double-blind period, participants received belumosudil 200 mg once daily, belumosudil 200 mg twice daily, or matched placebo.

The primary endpoint counted participants meeting the CRISS threshold at Week 24. The observed counts were 6 of 11, 3 of 12, and 7 of 12 for once-daily belumosudil, twice-daily belumosudil, and placebo, respectively. The registry’s logistic-regression intervals were broad and included the value corresponding to equal odds for both active-dose comparisons. Simple unadjusted risk-difference recalculations were also imprecise.

The record lists secondary outcomes and safety results, but important details of the original design rationale, full analysis plan, multiplicity strategy, and missing-data sensitivity analyses are not reported in the registry record. The primary findings are best read as uncertain estimates from the enrolled sample.