Efficacy and Safety of Riociguat in Patients With Systemic Sclerosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Riociguat in Patients With Systemic Sclerosis (NCT02283762), a randomized phase 2 study. The primary outcome is Change From Baseline in Modified Rodnan Skin Score (mRSS) to Week 52.

2. Clinical Question

The trial was intended to investigate whether riociguat is effective in systemic sclerosis. The primary endpoint focused on skin involvement, rather than treating a change within one group as sufficient evidence of a treatment difference. The key statistical comparison is the difference in change between the riociguat and placebo groups.

3. Trial Design

The registry identifies this as a Phase II, randomized, double-blind, placebo-controlled, parallel-group study of riociguat in participants with diffuse cutaneous systemic sclerosis. The sponsor was Bayer. The study enrolled 121 participants. Its recorded start date was 2015-01-15, its primary completion date was 2017-12-15, and its status is completed.

The main treatment phase lasted 52 weeks. In the riociguat group, participants received increasing doses, by 0.5 mg every 2 weeks, up to 2.5 mg 3 times a day. The titration period could last up to 10 weeks, followed by a maintenance period of up to 42 weeks. The placebo group received matching tablets with sham titration and a maintenance period described over the same time frame.

The arm descriptions also refer to a long-term extension phase beginning after completion of the main treatment phase in Week 52. Further details of the extension regimen are not reported in the registry record. The safety results distinguish the main treatment phase from the long-term extension phase, and those groups should be read as phase-specific records rather than as a single set of comparable treatment groups.

The primary endpoint was change from baseline in mRSS to Week 52. The outcome population was the full analysis set with evaluable data for this measure. The registry describes that set as participants randomized and treated with study medication who had evaluable outcome data. Although the record gives overall enrollment and outcome-specific group sizes, the original design assumptions, including the planned analysis population and sample-size justification, are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 139 patients were screened in 60 study centers in 15 countries worldwide. 121 patients of 139 patients were randomized and treated with at least one dose of study medication. 88 of the 121 randomized patients completed the treatment phase, of whom 87 entered the long term extension (LTE) phase.

Main Treatment Phase (MT)

Reasons for not completing this period:

Long-term Extension Phase (LTE)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS: all participants randomized and treated with study medication) with evaluable data for this outcome measure.

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 Change From Baseline in Modified Rodnan Skin Score (mRSS) to Week 52, measured over Baseline to week 52.

The primary endpoint was change from baseline in modified Rodnan Skin Score (mRSS) to Week 52. The mRSS is a physical examination method for estimating skin thickness. The registry describes it as validated and notes that it correlates with biopsy measures of collagen in the dermis and reflects prognosis and visceral involvement, especially in early disease.

The score uses ordinal assessments over 17 body areas, ranging from 0 (normal) to 3+ (severe induration), with a maximum score of 51. Higher scores indicate a worse situation. The endpoint is expressed as a mean change, so the direction of the change matters: the registry states that a decrease in mean change indicates improvement in mRSS.

This measure provides a way to quantify skin involvement over the treatment period. The treatment comparison concerns the difference between groups in their change from baseline, not simply whether either group’s average score declined. The outcome population was the full analysis set with evaluable data for this endpoint. The registry record does not report the details of how missing Week 52 measurements were handled in the primary analysis.

7. Results Posted in the Registry

• Riociguat (Adempas, BAY63-2521): mean -2.09 versus -0.77 on control; difference -1.32 (95% CI -4.00 to 1.36), standardized effect d = -0.19; z-test p = 0.335.

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.

Change From Baseline in Forced Vital Capacity (FVC) Percent Predicted to Week 52

• 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:
  • Riociguat (Adempas, BAY63-2521): mean -2.38 versus -2.94 on control; difference 0.57 (95% CI -2.76 to 3.90), standardized effect d = 0.07; z-test p = 0.737.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Riociguat (Adempas, BAY63-2521) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists five secondary outcomes: CRISS response at Week 52, HAQ-DI change, patient’s global assessment change, physician’s global assessment change, and FVC percent predicted change. Numerical results are available in the record for FVC percent predicted, but numerical results for the other listed secondary outcomes are not reported in the registry record. As a result, the overall pattern across all secondary endpoints cannot be characterized from the posted numerical information.

For FVC, the sponsor-reported 95% confidence interval includes zero, as does the interval from the unadjusted recalculation. The two estimates are imprecise and come from different methods. This result does not provide a clear, precise secondary signal that can be used to resolve the uncertainty around the primary mRSS result. Nor can the unreported secondary outcomes be treated as confirming or contradicting the primary result.

Secondary outcomes are useful for describing other dimensions of disease and functioning, but interpretation depends on the analysis plan and the number of comparisons made. When multiple outcomes are examined, the chance of at least one apparently notable result can increase if each is assessed separately without adjustment. The registry record does not report whether or how multiplicity was controlled. For that reason, any unadjusted secondary findings would generally carry less confirmatory weight than a prespecified primary analysis, and the missing numerical results further limit interpretation.

The secondary outcomes should therefore be read as additional questions the trial set out to assess, not as a unified body of evidence whose direction can be inferred from the primary result. The endpoint names alone do not reveal whether the results favored either group or how precise those estimates were. Those details are not reported in the registry record for the other listed secondary measures.

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

• CRISS (American College of Rheumatology Composite Response Index for Clinical Trials) at Week 52 Reported as Number of Participants With a CRISS Probability >=0.60 or <0.60 From Baseline to Week 52
• Change From Baseline in Health Assessment Questionnaire Disability Index (HAQ-DI) Score to Week 52
• Change From Baseline in Patient's Global Assessment Score to Week 52
• Change From Baseline in Physician's Global Assessment Score to Week 52
• Change From Baseline in Forced Vital Capacity (FVC) Percent Predicted to Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a continuous primary outcome: mean change in mRSS from baseline to Week 52, with standard deviations for each group. A mean describes the group’s average change, while the standard deviation describes variation among individual outcome values around that average. The two quantities answer different questions: the mean describes the average direction and size of change, and the standard deviation describes how dispersed the observed changes were.

What does the recalculated mean difference represent?

The unadjusted recalculation subtracts the placebo mean change from the riociguat mean change. For the primary outcome, the resulting estimate is -1.319. A negative difference means the observed average change was more negative in the riociguat group. Since the endpoint description says a decrease in mRSS indicates improvement, the point estimate corresponds to a larger average decrease in the riociguat group. This is a descriptive interpretation of the estimate, not a conclusion about causation or certainty.

The recalculation uses posted group summary statistics and is unadjusted. It does not reproduce a model that accounts for repeated measurements or other features of an individual-level analysis. The registry labels the sponsor’s primary analysis as MMRM, or a mixed model for repeated measures, and reports a difference of least-squares means. Least-squares means are model-based estimates; their values can differ from a direct comparison of the posted group means. The registry record does not report enough detail about the model specification, covariates, or missing-data assumptions to reconstruct that analysis.

How should the confidence interval be read?

A confidence interval gives a range of values that are reasonably compatible with the data under the specified statistical procedure and its assumptions. It communicates precision, rather than assigning a probability to the true effect being inside the particular interval. For the recalculated primary difference, the 95% confidence interval ranges from -3.998 to 1.36. Because that range includes zero, it does not exclude a zero between-group difference. Its width also shows that the estimate is uncertain. The sponsor-reported 95% interval, -4.99 to 0.30, likewise includes zero.

A p-value summarizes compatibility between the observed data and a null hypothesis under the assumptions of an analysis. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The recalculated primary p-value is 0.335; the sponsor-reported value is 0.082. The two values belong to different analyses, and the registry does not give enough detail to attribute their difference to a specific modeling choice.

Why do the two analysis results differ?

The recalculation is explicitly a simple, unadjusted comparison based on posted summary statistics. The sponsor’s reported analysis is an MMRM using least-squares means. Such analyses need not produce the same estimate or uncertainty because they are not the same calculation. The registry record does not report all the model details needed to explain the difference. There is no flagged discrepancy between the record and the recalculation, but the sponsor’s own analysis remains the trial’s reported model-based result and takes precedence in describing that analysis.

For FVC percent predicted, the same distinction applies. The unadjusted recalculation gives a mean difference of 0.569, with a 95% confidence interval from -2.758 to 3.896 and p = 0.737. The sponsor’s MMRM result is a difference in LS means of -0.20, with a 95% confidence interval from -3.40 to 3.00 and p = 0.901. The point estimates differ, and both reported intervals include zero. The registry does not provide sufficient model details to reconcile the values further.

Why can over-dispersion matter?

As a general statistical point, greater variation among participants makes an average difference harder to estimate precisely when the other features of a study are unchanged. For continuous outcomes, a larger standard deviation relative to the size of the mean difference generally produces greater uncertainty around a comparison. This is one reason to consider the group spreads as well as the mean values. It does not, by itself, determine whether a result is important or explain the study’s reported analysis.

The recalculated comparisons use pooled standard deviations as part of the simple summary-statistic approach. The registry record gives a pooled standard deviation of 7.01 for mRSS and 8.649 for FVC percent predicted. The recalculation is not a replacement for the sponsor analysis, and it should not be presented as the trial’s prespecified method. The record’s statistical plan and original assumptions for the main analysis are not reported in the registry record.

What can the analysis populations establish?

The primary outcome is described for a full analysis set of participants randomized and treated with study medication who had evaluable data for the outcome. This defines who contributed to the posted primary outcome, but it does not fully describe how all randomized participants were handled in the model. The outcome-specific group counts are 57.0 for riociguat and 52.0 for placebo. The FVC outcome counts are 55.0 and 51.0, respectively. These differing counts show that the reported outcome populations are not identical, but the reasons for missing or unevaluable data are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is reflected in the range of values compatible with an estimate, commonly expressed as a confidence interval. For the primary outcome, the unadjusted mean difference was -1.319, and its 95% confidence interval extended from -3.998 to 1.36. The interval includes zero and reaches values on both sides of zero. It therefore does not identify a single clear direction for the underlying between-group difference.

The sponsor’s MMRM estimate was -2.34, with a 95% confidence interval from -4.99 to 0.30. This interval also includes zero. Although the sponsor estimate is more negative than the unadjusted recalculation, the intervals overlap and both leave uncertainty about the size of the difference. These are not interchangeable analyses: the recalculation is unadjusted, whereas the sponsor result is model-based.

For FVC percent predicted, the recalculated difference was 0.569, with a 95% confidence interval from -2.758 to 3.896. The sponsor-reported difference in LS means was -0.20, with a 95% confidence interval from -3.40 to 3.00. Both intervals include zero and allow a range of possible between-group differences. Numerical estimates for other listed secondary outcomes are not reported in the registry record.

A confidence interval is not a guarantee that the true effect lies in its endpoints, and it does not describe the range of individual participant outcomes. It expresses uncertainty about an estimated group-level quantity under the method’s assumptions. The wide ranges relative to the point estimates indicate limited precision in these comparisons. The registry record does not report a clinical threshold for an important mRSS or FVC difference, so statistical uncertainty cannot be translated into a judgment about clinical importance from this record alone.

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 expressed as participants per arm, not total event counts. They use the observed effect as a starting point and show planning for 100%, 75%, or 50% of that effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For the continuous outcomes in this record, the figures are participants per arm.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the selected effect under the stated assumptions, if that effect is the true one. The 90% power column gives the corresponding planning target for a 90% chance. These are conventional design probabilities, not guarantees that a future study will detect an effect.

Planning for 100% of the observed primary effect gives 444 participants per arm for 80% power and 594 participants per arm for 90% power. Planning for 75% of the observed effect gives 789 participants per arm for 80% power and 1,056 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,774 participants per arm for 80% power and 2,375 participants per arm for 90% power. Smaller effects require more participants under these assumptions, because they are harder to distinguish from random variation.

These estimates are not the trial’s original design calculation: the original sample-size assumptions are not reported in the registry record. They are planning illustrations based on the observed effect, not observed power. They should be read as conditional estimates, not as a statement about the probability that this completed trial detected an effect.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.319; pooled standard deviation σ = 7.010.
2. n = 2 × (1.96 + 0.842)² × 7.010² / -1.319² = 443.4, rounded up to 444 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
delta <- -1.319                      # observed difference in means
sigma <- 7.01002318646425                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2283762)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 444 (80% power), 594 (90% power)
 75% of observed effect: n per arm = 789 (80% power), 1,056 (90% power)
 50% of observed effect: n per arm = 1,774 (80% power), 2,375 (90% power)
power.t.test: 444.4 
Simulated power at n = 444 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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

For the primary mRSS outcome, the sponsor reported an MMRM analysis with a difference of LS means of -2.34, a 95% confidence interval from -4.99 to 0.30, and p = 0.082. The unadjusted recalculation from the posted group means is -1.319, with a 95% confidence interval from -3.998 to 1.36 and p = 0.335. The sponsor estimate is more negative, but its interval includes zero, as does the recalculated interval.

The calculations differ because one is a model-based repeated-measures analysis and the other is a simple unadjusted recalculation from summary statistics. The registry record does not report enough detail to explain the difference in estimates or p-values more specifically. No discrepancy is flagged, and the sponsor’s own analysis takes precedence when describing the trial’s reported analysis.

The same distinction applies to the FVC outcome. The sponsor-reported difference in LS means is -0.20, with a 95% confidence interval from -3.40 to 3.00 and p = 0.901. The unadjusted recalculation is 0.569, with a 95% confidence interval from -2.758 to 3.896 and p = 0.737. The registry record does not provide the model specification needed to reconcile those estimates further. Neither analysis should be substituted for the other without making clear which method produced it.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, time point, or comparison. If each is tested separately, the chance of observing at least one result that appears unusual under a null model may increase. Statistical plans can address this issue through a hierarchy of endpoints, adjustment procedures, or other strategies, but the registry record does not report whether any such approach was specified or used.

The record lists a primary mRSS outcome and several secondary outcomes, including CRISS response, HAQ-DI, patient’s global assessment, physician’s global assessment, and FVC percent predicted. The available numerical secondary result is for FVC percent predicted; numerical results for the other listed outcomes are not reported in the registry record. Without the complete results and a reported multiplicity plan, secondary findings cannot be interpreted as a single confirmatory family of tests.

The primary analysis population is described as the full analysis set: participants randomized and treated with study medication who had evaluable data for the outcome. The record gives outcome-specific group counts, but it does not report detailed participant flow or reasons that data were unevaluable. It also does not report the assumptions or procedures used for missing outcome data in the sponsor’s MMRM analysis. A repeated-measures model can use available observations under its modeling assumptions, but the record does not state those assumptions or provide enough detail to assess them.

The registry identifies the sponsor’s method for the primary endpoint as MMRM and gives its estimate, interval, and p-value. The full statistical analysis plan, including covariate choices, handling of intercurrent events, sensitivity analyses, and any interim analyses, is not reported in the registry record. The original sample-size justification and design assumptions are also not reported. These omissions limit the ability to assess how closely the posted analyses follow the planned analysis strategy, but they do not justify assuming that any particular procedure was or was not used.

These limitations matter for interpretation: a reported estimate can be described, but confidence in its broader meaning depends on knowing the planned analysis, the outcome completeness, and how multiple questions were handled. The record supports cautious description of the reported primary result, while leaving these aspects of the analysis strategy unresolved.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: systemic scleroderma (4.4%), pericarditis (3.3%), pneumonia (3.3%), atrial fibrillation (2.4%), abdominal pain (2.4%).

The safety figures are reported separately for the main treatment phase and the long-term extension phase. During the main treatment phase, the riociguat group had 9 serious adverse events among 60 at risk, and the placebo group had 15 among 61 at risk. The record lists 1 death in each main-treatment group. These are phase-specific counts; they should not be combined with extension-phase counts.

In the long-term extension, the Riociguat-Riociguat group had 10 serious adverse events among 42 at risk, and the Placebo-Riociguat group had 11 among 45 at risk. The record lists 0 deaths for each extension group. The extension group labels and risk counts differ from those in the main treatment phase, so these figures should not be interpreted as a direct randomized comparison of the original treatment assignments.

The most frequently listed serious adverse event terms and percentages were systemic scleroderma (4.4%), pericarditis (3.3%), pneumonia (3.3%), atrial fibrillation (2.4%), abdominal pain (2.4%), and osteolysis (2.4%). The record’s safety data are descriptive and do not, on their own, establish that an event was caused by treatment or permit a complete assessment of comparative safety.

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

The primary result describes average change in mRSS over the main treatment period. The observed mean changes were decreases in both groups, and the estimated difference was more negative for riociguat than for placebo. The confidence intervals from both the unadjusted recalculation and the sponsor-reported analysis include zero. The estimates therefore do not provide a precise determination of the between-group difference.

This does not mean the groups were proven to be identical. A confidence interval that includes zero is compatible with no difference, but it can also include nonzero differences. Nor does the point estimate alone establish that riociguat caused a larger decrease. The result should be understood as an estimate with uncertainty, within the outcome population and time point recorded for this trial.

The findings also do not establish conclusions about every feature of systemic sclerosis. The primary endpoint measures skin thickness by mRSS; it is not a complete measure of disease status. The record lists additional outcomes, but results for all of them are not reported in the registry record. The available FVC result is also imprecise, and the record does not provide numerical results for the other listed secondary outcomes.

The sample-size illustrations are not evidence about whether this trial had enough participants to detect its actual effect. They are conditional planning calculations based on the observed effect and stated assumptions, rather than observed power or the original study justification. Safety counts likewise describe reported events in the named phases and groups; they do not establish causation or provide a complete benefit-risk assessment.

Overall, the registry record supports a careful account of the measured outcome, the posted estimates, and their uncertainty. It does not support a definitive claim that riociguat does or does not work, nor does it settle clinical importance. Such conclusions would require evidence beyond the statistical results and details available in this record.

18. Why This Trial Matters Statistically

This trial illustrates why a comparison between treatment groups is more informative than looking at change within one group alone. Both primary group means decreased, but the statistical question is whether the changes differ between groups and how precisely that difference is estimated. The recalculated mean difference and sponsor-reported model result provide distinct estimates, and each has an interval that includes zero.

It also demonstrates the importance of distinguishing an unadjusted recalculation from the trial’s reported analysis. The recalculation is transparent and can help readers understand the posted group summaries. The MMRM result is the sponsor’s model-based analysis. Their estimates and p-values are not identical, and the record does not provide enough modeling detail to explain every difference. Reporting the methods alongside the estimates is essential to avoid treating unlike analyses as if they were interchangeable.

Precision matters as much as the point estimate. The primary confidence intervals cover a range of possible differences, including zero, so the numerical result does not isolate a precise effect. The sample-size illustrations further show how planning requirements depend on the effect chosen: smaller effects require more participants under the stated assumptions. Those illustrations are not the trial’s original design rationale and do not measure the trial’s observed power.

Finally, the record underscores the limits of registry results when secondary numerical findings, missing-data details, multiplicity procedures, and the full analysis plan are not reported. A statistically careful reading separates what the record quantifies from what remains uncertain. This is especially important when assessing a Phase II study, whose estimates can inform further study planning but should not be treated as a definitive answer to a broad clinical question.

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 main limitation of the posted primary comparison is its uncertainty. The unadjusted confidence interval ranges from -3.998 to 1.36, and the sponsor-reported interval ranges from -4.99 to 0.30. Both include zero. The difference between the two estimates also warrants care: the unadjusted recalculation uses summary statistics, while the sponsor reports an MMRM analysis, and the registry does not provide enough detail to explain the difference.

The primary outcome population includes participants who were randomized and treated and had evaluable data for the outcome. The record does not provide a detailed account of missing measurements, reasons for missingness, or the assumptions used to handle missing data. Outcome-specific counts differ, and the registry record does not explain those differences.

Numerical results are not reported in the registry record for several listed secondary outcomes. This prevents assessment of their estimates, precision, and relation to the primary result. The record also does not report whether multiplicity was addressed, the full statistical analysis plan, the original sample-size justification, or the details needed to reproduce the sponsor’s model.

Safety results are separated by treatment phase. The long-term extension groups are not simply the original randomized groups maintained under the same comparison, so their counts should not be treated as a direct randomized contrast. The record gives event counts and selected serious-event terms, but these figures do not establish causality or provide all the context needed for a comprehensive safety comparison.

Finally, the primary result concerns mRSS change through Week 52 in a Phase II trial of participants with dcSSc. The registry record does not report a clinical threshold for meaningful change, and the available estimates should not be generalized beyond the study population, outcome, and follow-up described.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Riociguat in Patients With Systemic Sclerosis — NCT02283762.
• Registry record last updated 2020-02-05; status last verified 2020-01.
• Results first posted 2019-01-25.
• 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

NCT02283762 is a completed, randomized, double-blind, placebo-controlled Phase II parallel-group study of riociguat in diffuse cutaneous systemic sclerosis. The registry lists enrollment of 121 and Bayer as sponsor. The main treatment phase lasted 52 weeks, with riociguat dose titration and matching placebo.

The primary endpoint was change from baseline in mRSS to Week 52. The posted means decreased in both groups. The unadjusted recalculated difference was -1.319, with a 95% confidence interval from -3.998 to 1.36; the sponsor-reported MMRM difference of LS means was -2.34, with a 95% confidence interval from -4.99 to 0.30. Both intervals include zero.

The record also reports a sponsor analysis and an unadjusted recalculation for FVC percent predicted, and phase-specific safety counts. Numerical results for other listed secondary outcomes and several details of the planned statistical approach are not reported in the registry record.