Ravulizumab Versus Placebo in Adult Participants With Dermatomyositis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ravulizumab Versus Placebo in Adult Participants With Dermatomyositis (NCT04999020), a randomized phase 2, phase 3 study. The primary outcome is Number of Participants With International Myositis Assessment and Clinical Studies Total Improvement Score (IMACS-TIS) (TIS40) Response at Week 26 of the Randomized Controlled Period.

2. Clinical Question

The endpoint defines response as an IMACS-TIS score of at least 40 at Week 26. The comparison is based on participants in the randomized set, not on a general population of people with dermatomyositis. The posted counts are 9 participants with a response in the ravulizumab group and 6 in the placebo group; the corresponding group sizes are 26 and 12.

This is a question about a specific clinical score and assessment time. It does not, by itself, answer whether participants experienced improvement in every aspect of dermatomyositis, whether effects persisted beyond the reported period, or how the groups compared on safety. Those questions require other outcomes and adequate follow-up. The registry lists secondary outcomes covering clinical scores, skin activity, muscle enzymes, disease activity, muscle testing, and health assessment, but those measures do not replace the prespecified primary endpoint.

3. Trial Design

The registry describes a Phase 2/3, double-blind, randomized, placebo-controlled, parallel-group, multicenter study of ravulizumab in adults with dermatomyositis. The listed sponsor is Alexion Pharmaceuticals, Inc. The study began on 2021-11-19, and the primary completion date is 2023-10-26. Its status is terminated. The registry records enrollment of 38 participants.

In the randomized controlled period, 26 participants are listed in the ravulizumab group and 12 in the placebo group. The primary outcome uses the Randomized Set, defined in the registry as all randomized participants grouped by randomized treatment group. The intervention descriptions state that participants receive their assigned treatment in both Parts A and B. The posted primary outcome is assessed at Week 26.

Randomization and double masking are design features intended to support a fair comparison and limit the influence of expectations or knowledge of assigned treatment. A parallel-group design means participants are assigned to a group and the groups are compared over the study period. These are general explanations of the design terms; the registry record does not report the detailed procedures used to generate the allocation sequence, conceal assignment, or maintain masking.

The record does not report the original sample-size justification, the target enrollment, the planned allocation ratio, the reasons for termination, or the timing and rationale for any changes to the study. It also does not report the detailed protocol for Parts A and B. These items should not be inferred from the final enrollment or the group sizes in the posted results. The record describes additional open-label extension safety groups, but the detailed circumstances and follow-up represented by those groups 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: The study was planned to be conducted in 2 parts - Part A and Part B. The study was terminated early and participants were not enrolled into Part B. Therefore, results are presented for Part A of the study only. Part A consisted of a Randomized Controlled Period (RCP) and an Open-Label Extension (OLE) period.

Randomized Controlled Period (RCP)

Reasons for not completing this period:

Open-Label Extension (OLE) Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized Set, which included all randomized participants grouped by randomized treatment group.

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: Randomized Set, which included all randomized participants grouped by randomized treatment group.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With International Myositis Assessment and Clinical Studies Total Improvement Score (IMACS-TIS) (TIS40) Response at Week 26 of the Randomized Controlled Period, measured over Week 26.

The primary endpoint counts participants with an IMACS-TIS TIS40 response at Week 26. A response is defined as an IMACS-TIS score of at least 40. The registry characterizes TIS40 as a moderate improvement score.

IMACS-TIS combines six core set measures: physician global activity, patient global activity, extra-muscular disease activity, muscle strength, the Health Assessment Questionnaire, and muscle enzyme levels. The Total Improvement Score is formed from scores across these measures, taking account of improvement and the relative weight of each core set measure. The score ranges from 0 to 100, and a higher score indicates greater improvement.

A composite score can represent change across several clinically relevant domains rather than relying on a single measurement. That is the general rationale for using such an instrument. At the same time, a participant can reach a composite response threshold through different patterns of change across its components. The endpoint therefore does not show which individual component drove a response, and the count does not describe the full distribution of scores within either group.

The registry reports 9 responders among 26 participants assigned to ravulizumab and 6 among 12 assigned to placebo. These are the observed counts at the specified endpoint and time. The endpoint definition does not establish that every participant who met the threshold experienced improvement in every component, nor does it describe outcomes beyond Week 26.

7. Results Posted in the Registry

• RCP: Ravulizumab: 34.6% (9/26) versus 50.0% (6/12) on control; risk difference -15.4 percentage points (95% CI -49.1 to 18.3), risk ratio 0.69 (0.32–1.50); unadjusted two-proportion z-test p = 0.367.

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.

TIS at Week 26

• 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 errors.
• Result:
  • RCP: Ravulizumab: mean 31.16 versus 43.28 on control; difference -12.12 (95% CI -27.52 to 3.28), standardized effect d = -0.56; z-test p = 0.123.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCP: Ravulizumab and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline In Cutaneous Dermatomyositis Disease Area And Severity Index (CDASI) Activity Score at Week 26

• 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 errors.
• Result:
  • RCP: Ravulizumab: mean -3.80 versus -7.47 on control; difference 3.67 (95% CI -0.99 to 8.33), standardized effect d = 0.57; z-test p = 0.122.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCP: Ravulizumab and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Response Related to Muscle Enzymes: Normalization of Most Abnormal Baseline Enzyme at Week 26

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • RCP: Ravulizumab: 15.4% (4/26) versus 8.3% (1/12) on control; risk difference 7.1 percentage points (95% CI -13.9 to 28.0), risk ratio 1.85 (0.23–14.80); unadjusted two-proportion z-test p = 0.550.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCP: Ravulizumab and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures across several domains, including overall improvement, skin disease activity, muscle enzyme response, extra-muscular activity, global assessments, muscle testing, and health assessment. These outcomes can add context to the primary composite endpoint because they describe related but distinct aspects of disease activity and participant status. They should not be treated as interchangeable measures.

Among the secondary results with numeric estimates in the registry record, the pattern is mixed rather than uniformly favoring one group. The TIS mean estimate is lower for ravulizumab than placebo, and the CDASI change estimate is also less negative for ravulizumab; the muscle-enzyme normalization comparison has a positive risk-difference estimate for ravulizumab. The intervals for these recalculated comparisons include zero. This broad description does not establish a consistent effect across domains or explain the reasons for differences between endpoints.

These secondary results relate to the primary result by offering additional views of improvement and disease activity, but they do not override the primary endpoint. Measures may use different scales, definitions, and response thresholds, and may involve different available group sizes. The record lists 15 secondary outcomes, while the detailed statistical plan, the handling of missing secondary measurements, and any prespecified hierarchy among outcomes are not reported in the registry record.

Unadjusted secondary findings carry less weight when many outcomes are assessed because the chance of at least one apparently notable result can increase across multiple comparisons. This is a general statistical concern, not a claim that a particular correction was or was not applied by the sponsor. The registry does not report a multiplicity-control procedure. Secondary results are therefore most useful as descriptive context and as signals for further study, rather than as independent confirmatory evidence.

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

• TIS at Week 26
• Change From Baseline In Cutaneous Dermatomyositis Disease Area And Severity Index (CDASI) Activity Score at Week 26
• Number of Participants With Response Related to Muscle Enzymes: Normalization of Most Abnormal Baseline Enzyme at Week 26
• Change From Baseline In IMACS CSMs: Extra-Muscular Disease Activity Based on Myositis Disease Activity Assessment Tool (MDAAT) at Week 26
• Change From Baseline In IMACS CSMs: Physician Global Activity Assessment at Week 26
• Change From Baseline In IMACS CSMs: Patient Global Activity Assessment at Week 26
• Change From Baseline In IMACS CSMs: Manual Muscle Testing Subset 8 Muscles (MMT-8) at Week 26
• Change From Baseline In IMACS CSMs: Health Assessment Questionnaire (HAQ) at Week 26

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the TIS40 response definition at Week 26 or did not. For this kind of endpoint, the basic group summary is the number of participants meeting the definition and the number in the group. The posted counts are 9 of 26 for ravulizumab and 6 of 12 for placebo. A risk difference expresses the difference between the two response proportions. Its sign depends on the order of subtraction; the recalculation uses ravulizumab minus placebo.

What does the sponsor’s test assess?

The registry reports Barnard’s unconditional exact test for the difference in response rates. An exact test is designed for categorical outcomes and evaluates how compatible the observed counts are with a specified null comparison, using a probability model for the data. “Unconditional” describes the test’s approach to the possible group totals rather than conditioning on a fixed total number of responses. This is a general explanation of the method; the detailed implementation and all analysis settings are not reported in the registry record.

The sponsor analysis reports p = 0.419. A p-value is a measure, under the null model and the test assumptions, of how unusual data at least as incompatible with that null as the observed data would be. It is not the probability that the null hypothesis is true, and it does not measure the probability that a treatment effect is absent. The p-value also does not give the size or clinical importance of a difference; that is why the estimated difference and interval are important companion statistics.

What does the recalculation add?

The unadjusted recalculation uses the posted group counts to estimate a risk difference and its interval. It reports -0.154, with interval limits of -0.491 and 0.183, and an unadjusted p-value of 0.367. This calculation is not an adjusted model and does not incorporate participant-level data, covariates, or any details not represented in the posted counts. The confidence level and calculation method for this recalculated interval are not reported in the registry record.

“Unadjusted” means that the calculation compares the groups without adjustment for other measured variables or a broader model. It is useful as a transparent summary check, but it may not reproduce an analysis that uses a different test, model, or analysis population. The sponsor’s reported analysis is the primary record-based analysis; the recalculation should be interpreted alongside it, not substituted for it.

How should precision be considered?

A confidence interval describes a range of estimates compatible with the data under a specified statistical procedure. In general, narrower intervals indicate greater precision and wider intervals indicate less precision. For a difference, an interval that includes zero does not establish a clear direction of difference at the interval’s stated confidence level. The sponsor’s interval is explicitly reported as 80%; its bounds extend from -38.55 to 8.48. The recalculated interval also spans zero, but its confidence level is not stated in the registry record.

Small group sizes and limited outcome counts can make estimates imprecise. Exact methods are often considered for sparse binary outcomes because large-sample approximations can be unreliable when counts are limited. This is a general reason such methods may be selected; the registry does not state the sponsor’s rationale for choosing Barnard’s test.

How do the continuous secondary outcomes differ?

The registry also reports least-squares means and standard errors for continuous secondary outcomes, including TIS and change in CDASI activity score. A mean summarizes the average score or change in a group, while a standard error describes uncertainty in the estimated mean. The recalculated mean differences use the posted group summaries. For those calculations, the pooled standard deviation is described as approximate, derived from the reported standard errors. That approximation and the limited group sizes should be kept in mind when interpreting the recalculated intervals and planning illustrations.

For binary secondary outcomes, such as normalization of the most abnormal baseline muscle enzyme, the reported count can be compared through a risk difference. The same broad cautions apply: the point estimate describes the observed comparison, while the interval conveys uncertainty, and a p-value alone does not establish the importance or reliability of an effect.

What is not documented?

The registry does not report a detailed statistical analysis plan, the original sample-size justification, the confidence level and method for every recalculated interval, or the handling rules for missing endpoint measurements. It does not report whether interim analyses were planned or conducted, nor does it describe a multiplicity-control procedure. Those details cannot be reconstructed from the posted summary results and should not be assumed.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.154, with interval limits of -0.491 and 0.183. The interval spans zero, so the posted data do not pin down the direction of the underlying difference with precision. The estimate is also compatible with a range of magnitudes on either side of zero. The confidence level and method attached to this recalculated interval are not reported in the registry record.

The sponsor’s reported interval is explicitly an 80% confidence interval: -38.55 to 8.48 for the reported difference in response rates of -15.38. It too spans zero. Because the reported sponsor interval and the recalculated risk-difference interval are presented using different numerical scales and the recalculated interval’s confidence level is not stated, they should not be treated as interchangeable bounds. The sponsor’s p-value is 0.419; the recalculated unadjusted p-value is 0.367.

In general, a confidence interval reflects both the observed estimate and the uncertainty created by sampling. A wide interval means the data remain compatible with a broad range of possible differences. It does not mean that all values in the interval are equally likely, and it does not guarantee that the true effect lies within the particular interval.

The group sizes and responder counts are limited, which is relevant to precision. The posted point estimate should therefore not be read as a stable estimate of the size of a treatment effect. The registry also does not report enough detail to assess how missing measurements, if any, affected the endpoint analysis. The interval communicates uncertainty under its calculation method, but it cannot answer questions that depend on unreported analysis or follow-up information.

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 participants per arm, not total participants or total events. The sample-size assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one and the model assumptions held. The 90% column gives the corresponding planning target for a 90% chance. These are repeated-study operating characteristics under assumptions, not guarantees for an individual trial.

The rows that plan for 75% or 50% of the observed effect represent smaller effects than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the planning illustration requires more participants per arm. The listed figures are illustrations derived from the observed effect, not the design basis reported for the terminated trial. They are not observed power: observed power is not a useful substitute for interpreting the estimate, its uncertainty, and the trial’s actual design.

For continuous outcomes, the planning calculations use approximate variability derived from posted summaries, as described with the recalculated comparisons. For the primary binary outcome, the figures are also planning illustrations based on the observed difference. They should be read as conditional scenarios, not as evidence that a future study will reproduce the observed effect or achieve a particular result.

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 = 0.500; treatment proportion p₁ = 0.346; average p̄ = 0.423.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6987 = 1.3694.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6902 = 0.5809.
4. n = (1.3694 + 0.5809)² / (-0.1538)² = 160.7, rounded up to 161 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 <- 0.5                          # control proportion
p1 <- 0.346153846153846                          # 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(4999020)
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 = 161 (80% power), 215 (90% power)
 75% of observed effect: n per arm = 290 (80% power), 388 (90% power)
 50% of observed effect: n per arm = 659 (80% power), 881 (90% power)
power.prop.test: 160.7 
Simulated power at n = 161 per arm: 0.792 (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 sponsor’s reported primary analysis is Barnard’s unconditional exact test. It gives a difference in response rates of -15.38, an 80% confidence interval from -38.55 to 8.48, and p = 0.419. These are the registry’s reported inferential results and should take precedence when describing the sponsor’s analysis.

The unadjusted recalculation uses the posted counts of 9 responses among 26 participants assigned to ravulizumab and 6 among 12 assigned to placebo. It estimates a risk difference of -0.154, with interval limits of -0.491 and 0.183, and an unadjusted p-value of 0.367. The recalculation provides a simple comparison based on summary counts. It is not an attempt to reproduce all details of the sponsor’s analysis, and its interval is not reported with a confidence level in the registry record.

The two p-values differ because the calculations are not identical analyses. The registry marks the discrepancy flag as false, so the sponsor result is not identified as discrepant in the record. The recalculated values can help readers understand the posted counts, but they do not supersede the sponsor’s specified exact test or establish a different conclusion. Both sets of results indicate uncertainty, and neither should be interpreted without the point estimate and interval.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, or comparisons. Even if each test is interpreted using its own nominal threshold, examining many results can make an apparently unusual result more likely to occur by chance somewhere among them. Methods such as a prespecified hierarchy or a statistical adjustment can address this issue, but the registry record does not report a multiplicity-control procedure or a hierarchy for the outcomes.

The record lists 16 outcome measures and 15 posted secondary outcomes. The primary endpoint is the TIS40 response at Week 26; several secondary outcomes cover related clinical domains. Without a documented analysis plan, it is not possible to determine from the registry record which outcomes were intended to be confirmatory, whether testing order was prespecified, or whether any adjustment was applied. The unadjusted secondary comparisons should accordingly be interpreted as exploratory or descriptive unless other documentation establishes their role.

Missing data also matter because the primary endpoint is assessed at Week 26. The registry defines the primary population as the Randomized Set, but does not report the detailed rules used for missing Week 26 assessments, withdrawals, or other unavailable measurements. It does not describe an imputation method, a sensitivity analysis, or how participants without endpoint data were handled. The reported group counts alone do not resolve those questions.

The safety record lists risk-set sizes that differ across the randomized and open-label extension groups. The reason for these denominators, the periods of observation they represent, and the rules for assigning participants to those safety groups are not reported in the registry record. They should not be assumed to match the primary efficacy population.

The registry also does not report whether interim analyses were planned or conducted, how the termination decision affected the analysis, or whether any changes were made to the statistical plan. These omissions limit assessment of the analysis process, but they do not by themselves show that a particular bias occurred. Interpretation should stay with the stated endpoint, population, and posted results while recognizing these unanswered design and analysis questions.

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: anaemia (11.1%), escherichia urinary tract infection (11.1%), cardiac failure (11.1%), coronary artery stenosis (11.1%), myocardial infarction (11.1%).

For the randomized controlled period, the safety record lists serious adverse events for 2 participants among 25 at risk in the ravulizumab group and 0 among 13 at risk in the placebo group. It lists other adverse events for 9 among 25 at risk in the ravulizumab group and 10 among 13 at risk in the placebo group. No deaths are listed in either randomized-period group.

The open-label extension entries are reported separately: 4 serious adverse events among 22 at risk and 11 other adverse events among 22 at risk for ravulizumab to ravulizumab; 4 serious adverse events among 9 at risk and 7 other adverse events among 9 at risk for placebo to ravulizumab. No deaths are listed in either extension group. These groups should not be combined with, or interpreted as direct randomized comparisons against, the placebo group without details of exposure and follow-up.

The registry identifies Anaemia, Escherichia urinary tract infection, Cardiac failure, Coronary artery stenosis, Myocardial infarction, and Intestinal haemorrhage among the listed serious terms, each with 11.1%. The safety summaries are counts and listed terms, not a complete assessment of comparative risk. The record does not report the exposure duration, event timing, or detailed criteria needed to judge these counts in context.

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

The primary endpoint records whether participants met a defined threshold on the IMACS-TIS at Week 26. The posted results show 9 responders among 26 participants in the ravulizumab group and 6 among 12 in the placebo group. The recalculated risk difference is -0.154, and its interval spans zero. The sponsor’s reported exact-test analysis also has an interval spanning zero and reports p = 0.419.

These results describe the observed groups in this terminated trial. They do not establish that ravulizumab caused a lower or higher response rate, prove that the treatments have identical effects, or determine what would happen in a larger or different population. An uncertain estimate is not evidence of equivalence. Demonstrating equivalence or noninferiority would require an appropriate design, margin, and analysis; those are not reported.

The response threshold is one composite endpoint. It does not show how each core set measure changed, whether every participant had improvement in each domain, or whether changes were maintained beyond Week 26. Secondary outcomes can provide complementary information, but their unadjusted findings are subject to uncertainty and multiplicity concerns, and the registry does not report a procedure controlling for multiple comparisons.

The safety counts likewise describe events recorded in the listed groups. Differences in group size, unreported exposure time, and the separate open-label extension groups limit simple comparisons. The posted safety information should not be read as a complete estimate of comparative safety or as proof that an event is or is not related to study treatment.

Overall, the registry record supports a cautious description of the measured endpoint and its uncertainty. It does not provide enough detail to resolve the reasons for termination, missing-data handling, the original design assumptions, or the full analysis plan. Those matters are relevant to interpretation and should remain explicit uncertainties rather than being filled in by inference.

18. Why This Trial Matters Statistically

This study illustrates why a clinical-trial result should be read through the combination of an endpoint definition, an effect estimate, an interval, and the analysis method. A simple count of responders does not convey the difference’s precision. The recalculated risk difference and the sponsor’s exact-test result both show why a point estimate alone is insufficient: the data leave substantial uncertainty about the direction and size of the comparison.

It also highlights the distinction between an analysis reported by a sponsor and a simple unadjusted recalculation from summary counts. The recalculation can make the arithmetic comparison transparent, while the registry’s Barnard exact test remains the sponsor’s reported analysis. Understanding their different methods helps prevent a recalculated p-value from being mistaken for the original trial analysis.

The trial’s status and enrollment make design context important. The registry records a terminated study with enrollment of 38, but does not report the reason for termination or the original sample-size justification. The planning illustrations derived from the observed effect cannot fill that gap. They show how assumptions about effect size and target power influence hypothetical study size, not what the original investigators planned.

Finally, the endpoint is a composite clinical score and the study lists multiple secondary domains. Statistical interpretation must distinguish the primary result from secondary signals, account for multiplicity, and recognize that unreported details about missing data and follow-up limit assessment. These are general lessons in evaluating registry results: statistical evidence is conditional on the design, measurements, and analysis that generated it.

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 registry record leaves several trial-specific questions unanswered. It reports termination but not the reason, whether the decision affected enrollment or follow-up, or whether all planned assessments were completed. The record gives an enrollment of 38, but does not report the original target enrollment or sample-size justification. Planning illustrations based on the observed effect are not a substitute for those design details.

The primary efficacy population is described as the Randomized Set, but the record does not explain how missing Week 26 data were handled or whether sensitivity analyses were conducted. The randomized-period safety denominators also differ from the efficacy group sizes, and the reason for this difference is not reported. Exposure duration and the timing of adverse events are not provided in the listed summaries.

The sponsor’s primary analysis is reported, but a detailed statistical analysis plan is not. The record does not describe an adjustment for multiple secondary comparisons, an outcome hierarchy, interim analyses, or whether the reported analyses were changed after study initiation. These missing details limit evaluation of the analysis choices without establishing that a particular problem occurred.

The primary endpoint is a composite score threshold, so the responder count does not reveal the component-level pattern of change. Follow-up beyond the Week 26 primary assessment and the durability of responses are not reported in the primary result. The open-label extension safety entries are separate from the randomized comparison and lack the exposure and follow-up detail needed for a direct comparative interpretation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ravulizumab Versus Placebo in Adult Participants With Dermatomyositis — NCT04999020.
• Registry record last updated 2025-07-09; status last verified 2025-07.
• Results first posted 2024-12-06.
• 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

NCT04999020 is a Phase 2/3, randomized, double-blind, placebo-controlled, parallel-group, multicenter study of ravulizumab in adults with dermatomyositis. The registry lists Alexion Pharmaceuticals, Inc. as sponsor, enrollment of 38, and terminated status.

The primary outcome is the number of participants with an IMACS-TIS TIS40 response at Week 26. The posted counts are 9 among 26 participants assigned to ravulizumab and 6 among 12 assigned to placebo. The sponsor reports Barnard’s unconditional exact test, a difference in response rates of -15.38, an 80% confidence interval from -38.55 to 8.48, and p = 0.419. The unadjusted recalculation gives a risk difference of -0.154, interval limits of -0.491 and 0.183, and p = 0.367.

The registry lists multiple secondary outcomes and safety results, but does not report the reason for termination, the original sample-size justification, detailed missing-data methods, or a multiplicity-control procedure. The posted primary comparison is uncertain and should be interpreted with these limits in mind.