A Study to Evaluate the Efficacy, Safety, and Pharmacokinetics of IgPro20 in Adults With Dermatomyositis (DM): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy, Safety, and Pharmacokinetics of IgPro20 in Adults With Dermatomyositis (DM) (NCT04044690), a randomized phase 3 study. The primary outcome is Responder Rate.

2. Clinical Question

The responder definition requires a Total Improvement Score of at least 20 points at Week 25 and at least one previous scheduled visit, Week 17 or Week 21. It also requires completion of 24 weeks of randomized treatment without rescue corticosteroid treatment. The score combines six weighted core-set measures used in international myositis assessment: Physician and Patient Global Disease Activity, Manual Muscle Testing-8, Health Assessment Questionnaire, Muscle Enzyme, and Extramuscular Global Activity. The question is therefore not simply whether a score crossed a threshold at one visit; the definition also incorporates earlier assessment and treatment-course conditions.

The registry record identifies the primary outcome as the percentage of participants who were responders at Week 25. It also lists secondary assessments of Total Improvement Score, muscle testing, skin disease activity, corticosteroid reduction, and rescue steroid treatment. These outcomes add context to the primary responder comparison, but they do not change what the primary question measures.

3. Trial Design

The RECLAIIM study is listed as a phase 3, randomized, parallel-group study of IgPro20 in adults with dermatomyositis. Its brief description calls it multicenter, placebo-controlled, and double-blind. The registry’s masking classification is quadruple. These are the record’s descriptions; which trial roles were masked is not reported in the registry record.

The two arms were IgPro20 and placebo. IgPro20 was human immunoglobulin G administered subcutaneously, while placebo was a human albumin solution administered subcutaneously. The registry lists enrollment as 134. The primary outcome analysis reports 65 participants in each arm; this analysis count should not be assumed to describe every analysis population or the full pattern of trial participation.

The study started on 2019-10-21, and its primary completion date is listed as 2024-12-02. Its current registry status is terminated. The reason for termination and its implications for the planned conduct are not reported in the registry record. The record’s primary objective was to compare IgPro20 with placebo on responder status based on Total Improvement Score assessments.

The primary result is presented for the modified intent-to-treat analysis set. The registry describes this set as participants who underwent screening and were randomized to receive any amount of randomized investigational medicinal product. The remaining text of the population definition is incomplete, so additional eligibility or exclusion details are not reported in the registry record. Multiple imputation was used for missing primary-outcome values among participants who discontinued because of military activities in Ukraine. The registry does not report the original trial design assumptions or a complete account of the analysis plan.

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 199 participants were screened, and 65 of these were screen failures. A total of 134 were randomized in the study. This study consisted of 3 study periods (SP): SP1 (from Baseline to Week 25), SP2 (from Week 25 to 56) and SP3 (from Week 56 to approximately 5 years, study drug reimbursement was planned until drug becomes commercially available or if there is no longer benefit from the study drug). However, the study was terminated early.

Period 1

Reasons for not completing this period:

Period 2

Reasons for not completing this period:

Period 3

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on the modified intent-to-treat (mITT) analysis set. The mITT analysis set comprises all participants who underwent study screening procedures, were randomized to receive any amount of randomized IMP. The documented failure to take any amount of randomized IMP or the lack of any post randomization efficacy data lead to the exclusion of the participant from the mITT.

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 the safety (SAF) analysis set. The SAF analysis set comprised all participants who were randomized and received any amount of randomized investigational medicinal product (IMP) and were based on the actual treatment sequence received. Here, baseline characteristics are reported for Period 1, as participants from this cohort were selected to proceed to Periods 2 and 3.

6. Primary Endpoint

The registry lists the primary outcome as Responder Rate, measured over At Week 25.

The primary endpoint is the percentage of participants classified as responders at Week 25. A responder had to reach a Total Improvement Score of at least 20 points at Week 25 and at least one of the preceding scheduled visits, Week 17 or Week 21, while completing 24 weeks of randomized investigational treatment without rescue corticosteroid treatment.

Total Improvement Score combines six weighted core-set measures: Physician and Patient Global Disease Activity, Manual Muscle Testing-8, Health Assessment Questionnaire, Muscle Enzyme, and Extramuscular Global Activity. The registry identifies thresholds of 20, 40, and 60 points as minimal, moderate, and major improvement, respectively. The primary endpoint uses the threshold of at least 20 points, together with the timing and treatment-course conditions in the responder definition.

A responder endpoint can be useful because it translates a multi-measure assessment into the proportion of participants who satisfy a prespecified clinical response definition. It is also easy to express as a comparison between groups. However, reducing a score to responder or non-responder status discards information about how far participants’ scores moved and how close non-responders came to the threshold. The registry lists mean Total Improvement Score and other assessments among secondary outcomes, which can provide complementary information when their results are reported.

The Week 25 outcome was analyzed in the modified intent-to-treat population. The registry says multiple imputation was used for missing values among participants who discontinued due to military activities in Ukraine; other details of missing-data handling are not reported in the registry record.

7. Results Posted in the Registry

• IgPro20: 64.6% (42/65) versus 61.5% (40/65) on control; risk difference 3.1 percentage points (95% CI -13.5 to 19.7), risk ratio 1.05 (0.81–1.37); unadjusted two-proportion z-test p = 0.716.

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.

Percentage of Participants Who Are Able to Reduce the Oral Corticosteroid Dose by >= 25%

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • IgPro20: 23.1% (15/65) versus 20.0% (13/65) on control; risk difference 3.1 percentage points (95% CI -11.0 to 17.2), risk ratio 1.15 (0.60–2.23); unadjusted two-proportion z-test p = 0.670.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IgPro20 and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Meeting DOW and Receiving Rescue Steroid Treatment

• 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:
  • IgPro20: 0.0% (0/65) versus 3.1% (2/65) on control; risk difference -3.1 percentage points (95% CI -7.3 to 1.1); unadjusted two-proportion z-test p = 0.154.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IgPro20 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Meeting DOW and Receiving Rescue Steroid Treatment

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • IgPro20: 0.0% (0/65) versus 3.1% (2/65) on control; risk difference -3.1 percentage points (95% CI -7.3 to 1.1); unadjusted two-proportion z-test p = 0.154.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IgPro20 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several dimensions of dermatomyositis assessment, including Total Improvement Score, Manual Muscle Testing-8, skin disease activity, oral corticosteroid reduction, and rescue steroid treatment. This breadth can help show whether the primary responder comparison is accompanied by a consistent pattern across related measures. The registry lists 34 outcome measures and 33 secondary outcomes posted, but detailed results for many of the listed outcomes are not reported in the registry record.

For the secondary results with figures available, the observed directions are not a substitute for a coherent overall pattern across all measures. The corticosteroid-reduction endpoint and rescue-treatment endpoints are distinct from the primary responder definition, even though rescue treatment is also part of that definition. They should be interpreted according to their own outcome definitions and analysis populations rather than treated as independent confirmations of the primary endpoint.

Secondary outcomes can support interpretation by adding information about function, skin activity, score trajectories, or treatment changes. They do not overturn an uncertain primary comparison, and a result on one secondary measure does not establish a broad effect across the other domains. The registry does not report a multiplicity adjustment or a prespecified testing hierarchy. When many outcomes are examined without a reported plan for controlling false-positive findings, individual unadjusted results carry less weight and are more appropriately treated as exploratory.

The registry record also does not report enough statistical detail to evaluate how all secondary analyses handled missing observations, repeated assessments, or dependence among outcomes. The safest reading is that the secondary endpoints provide additional context where results are posted, while the primary Week 25 responder result remains the central comparison.

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

• Mean TIS
• Mean Changes From Baseline in MMT-8
• Mean Changes From Baseline in Cutaneous Dermatomyositis Disease Area and Severity Index Total Activity Score (CDASI-A)
• Percentage of Participants Who Are Able to Reduce the Oral Corticosteroid Dose by >= 25%
• Period 1: Mean TIS at Each Visit
• Period 2: Mean TIS at Each Visit
• Period 1: Percentage of Participants Achieving TIS ≥ 20, ≥ 40 and ≥ 60 Points
• Period 2: Percentage of Participants Achieving TIS ≥ 20, ≥ 40 and ≥ 60 Points

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary for each participant: the participant either met the responder definition or did not. The arm-level percentage describes the share classified as responders. A comparison of these percentages can be expressed as an absolute difference, a relative risk, or an odds ratio. These measures answer related but distinct questions and use different scales.

The unadjusted recalculation reports a risk difference of 0.031 for IgPro20 compared with placebo. A risk difference is the difference between the two observed proportions, expressed on the probability scale. A value of zero corresponds to equal proportions. The recalculated 95% confidence interval extends from -0.135 to 0.197, so it includes zero and allows for effects in either direction. The recalculation is based on posted summary statistics and is not a replacement for the sponsor’s analysis.

The registry reports the sponsor’s analysis as logistic regression, with an odds ratio of 1.13 and a 95% confidence interval from 0.551 to 2.309. Logistic regression models the odds of a binary outcome. An odds ratio of 1 is the no-association value. Odds ratios are not risk differences: when outcome proportions are not rare, the two measures can differ substantially in interpretation and magnitude. The registry does not report enough detail to reconstruct the full regression model or determine which covariates, if any, were included.

A p-value summarizes how incompatible observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The recalculated unadjusted p-value is 0.716. The sponsor’s reported p-value is recorded with more digits than permitted for display, so it is not reproduced. Both the confidence intervals and the p-values should be considered alongside the effect estimates rather than treated as stand-alone conclusions.

General statistical note: A confidence interval reflects sampling uncertainty under a statistical model and a particular analysis. It does not account automatically for every possible source of bias, such as incomplete follow-up, outcome misclassification, or limitations in how a trial was conducted. An interval that includes the no-effect value indicates that the data are compatible with no difference under that analysis, but it can also include potentially meaningful differences in either direction.

General statistical note: Binary outcomes convert each participant’s experience into a category. This can make results straightforward to communicate, but it loses detail that may be retained in a continuous score. The responder definition also combines several conditions, so a participant can fail to qualify for more than one reason. The posted arm-level responder percentages alone do not show which component of the definition was most influential.

The primary endpoint uses the modified intent-to-treat population. The registry says that this population comprises participants who underwent screening and were randomized to receive any amount of randomized investigational medicinal product. The definition as recorded ends before the full eligibility statement is complete. The complete analysis-population definition, including any further exclusions, is not reported in the registry record. This limits the ability to assess how closely the analyzed population corresponds to all randomized participants.

For missing primary-outcome values, the registry reports multiple imputation for participants who discontinued because of military activities in Ukraine. Multiple imputation is a general statistical approach that replaces missing values with values drawn from a model, then combines results across completed data sets to reflect uncertainty about the missing observations. Its validity depends on the assumptions and variables used in the imputation model. The variables, model specification, number of imputations, and treatment of other missing values are not reported in the registry record.

General statistical note: Missingness can matter when the probability of an unobserved outcome is related to the outcome itself or to other participant characteristics. Imputation can address missing data only to the extent that its assumptions and model are reasonable. A reported use of multiple imputation does not, by itself, establish that missing-data bias has been eliminated. The registry record does not report sensitivity analyses for the primary outcome.

The primary result is a comparison between randomized arms, but the record’s brief description and outcome information do not establish every detail of implementation. Randomized allocation is intended to reduce systematic differences between groups at baseline. Masking can help limit differences in care, outcome assessment, or participant reporting. The registry lists quadruple masking while the brief study description says double-blind; the exact masked roles and procedures are not reported in the registry record. The allocation sequence method and concealment details are also not reported in the registry record.

The primary responder result should be distinguished from the secondary outcomes. The registry lists 34 outcome measures and 5 analyses, with 33 secondary outcomes posted. Multiple outcomes can be informative, but examining many endpoints increases the opportunity for chance findings. Adjustment for multiplicity, a prespecified hierarchy, and the complete statistical analysis plan are not reported in the registry record. General statistical practice treats isolated secondary findings cautiously when the multiplicity strategy is unknown.

General statistical note: Over-dispersion is relevant in analyses of counts or rates when variation exceeds the assumptions of a simple probability model. It can lead to standard errors that are too small if ignored. The primary endpoint is a binary responder outcome, not a count-rate outcome, and the registry does not report an over-dispersion analysis for it. That concept should not be confused with the uncertainty captured by the reported confidence interval.

The sponsor’s regression result and the recalculation are not identical analyses. The sponsor reports an odds ratio from logistic regression, whereas the recalculation reports an unadjusted difference in proportions. Different effect measures and modeling choices can yield different estimates and p-values. The record does not provide enough model detail to attribute the difference to a particular adjustment or specification. Since the registry does not flag a discrepancy, the two results are best read as complementary summaries with distinct methods, not as interchangeable numbers.

11. Confidence Intervals and Precision

The primary arm estimates are reported as 64.3% for IgPro20, with a 95% confidence interval from 52.56% to 75.99%, and 61.6% for placebo, with a 95% confidence interval from 49.52% to 73.74%. These intervals are broad: each is compatible with a range of responder proportions rather than a single precise value. The overlap between the arm-specific intervals is not itself a formal test of the treatment difference; the direct comparison and its confidence interval are more relevant for that question.

The unadjusted risk difference is 0.031, with a 95% confidence interval from -0.135 to 0.197. Because this interval includes zero, the data are compatible with no difference in responder proportions. It also extends into both negative and positive values, so the data are compatible with a difference favoring either arm. The estimate is not precise enough to rule out a broad range of possible contrasts.

Confidence intervals are often described as a measure of precision: narrower intervals indicate less sampling uncertainty under the model used. They are not guarantees that the true value lies within the interval, nor do they account for biases or unreported design features. The sponsor’s odds ratio interval, from 0.551 to 2.309, also spans its no-association value of 1 and leaves substantial uncertainty on the odds scale.

Precision should be judged against the clinical meaning of the responder definition and the range of effects that would matter, not by whether an estimate is positive or negative alone. The registry does not report a threshold for a clinically important between-arm difference. The observed estimates therefore cannot be classified against such a threshold from 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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For this binary responder outcome, the figures are participants per arm. They are not total participants across the trial. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The original sample-size justification and assumptions are not reported in the registry record.

The columns for 80% and 90% power describe the number of participants per arm that the illustration estimates would be needed to have the stated probability of detecting an effect of the chosen size, if that effect were real and the assumptions held. For example, using 100% of the observed effect gives planning estimates of 3,861 participants per arm for 80% power and 5,168 participants per arm for 90% power. The higher power target requires a larger planned sample under the same assumptions.

Rows that plan for 75% or 50% of the observed effect posit smaller effects to detect. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm in this calculation. These are hypothetical planning scenarios, not trial outcomes and not evidence that a future study would achieve its target.

These figures are not observed power. They are prospective calculations based on an effect estimate from the posted results. Because that estimate is uncertain, planning based directly on it can yield unstable sample-size figures. The record does not report whether these illustrations were used in planning the trial.

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 = 0.615; treatment proportion p₁ = 0.646; average p̄ = 0.631.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6825 = 1.3377.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6821 = 0.5741.
4. n = (1.3377 + 0.5741)² / (0.0308)² = 3,860.5, rounded up to 3,861 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 <- 0.615384615384615                          # control proportion
p1 <- 0.646153846153846                          # 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(4044690)
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 = 3,861 (80% power), 5,168 (90% power)
 75% of observed effect: n per arm = 6,894 (80% power), 9,228 (90% power)
 50% of observed effect: n per arm = 15,575 (80% power), 20,850 (90% power)
power.prop.test: 3860.5 
Simulated power at n = 3,861 per arm: 0.800 (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 posted analysis uses logistic regression and reports an odds ratio of 1.13 for IgPro20 compared with placebo, with a 95% confidence interval from 0.551 to 2.309. The interval includes 1, the no-association value for an odds ratio. The reported analysis therefore does not establish a clear difference on the odds scale.

The recalculation uses the arm-level responder summaries to estimate an unadjusted risk difference of 0.031, with a 95% confidence interval from -0.135 to 0.197 and an unadjusted p-value of 0.716. This is an absolute difference in proportions, not an odds ratio. The sponsor’s reported p-value is not reproduced because it has more than three decimal places in the registry record.

The sponsor’s estimate and the recalculated estimate need not match numerically: they use different effect measures, and the sponsor reports a regression analysis while the recalculation is unadjusted. The registry does not report sufficient model details to identify the exact reasons for any difference. Both results leave uncertainty about the between-arm effect. The registry record does not flag a discrepancy between the analyses.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and numerous secondary outcomes. Testing multiple outcomes can increase the chance that at least one result appears unusual by chance, even when no underlying difference exists. Statistical methods such as adjustment of significance thresholds, control of the false discovery rate, or a prespecified testing sequence can address aspects of this problem. Whether any such strategy was used is not reported in the registry record.

The record lists 34 outcome measures, 5 analyses, and 33 secondary outcomes posted. These counts describe the registry record, not the number of independent statistical tests performed. Outcomes may be related, and repeated assessments may be correlated. The full analysis plan, endpoint hierarchy, and multiplicity procedures are not reported in the registry record. Consequently, secondary p-values should not be read as if each were the sole planned test.

Missing-data handling is partly described for the primary endpoint: multiple imputation was used for participants who discontinued due to military activities in Ukraine. The registry does not report the imputation model, variables used, number of imputed data sets, or sensitivity analyses. Handling of missing values for other outcomes is not reported in the registry record. Because responder status requires an assessment at specified visits and completion of a treatment period without rescue corticosteroid treatment, missing or incomplete follow-up may affect classification; the registry record does not provide enough detail to assess that issue fully.

The primary analysis population is described as a modified intent-to-treat set involving screening and randomization to receive any amount of randomized investigational medicinal product. The recorded definition is incomplete. The full criteria for inclusion and any exclusions are not reported in the registry record. This makes it difficult to assess exactly how the analysis set relates to all randomized participants or whether the same population was used for each endpoint.

The registry also does not report a complete account of interim analyses, stopping rules, or the trial’s original statistical plan. These details should not be inferred from the terminated status. The reason for termination is not reported in the registry record.

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: covid-19 (5.9%), covid-19 pneumonia (3.0%), pneumonia (2.9%), urinary tract infection (2.9%), cystitis (2.9%).

The registry reports serious adverse events by treatment sequence and period. In Period 1, the IgPro20 sequence lists 3 participants with serious adverse events among 67 at risk, and the placebo sequence lists 5 among 67 at risk. Later-period entries are reported for sequences that include continued or subsequent IgPro20 exposure. Because treatment histories differ across these periods, they should not be treated as a simple parallel-arm comparison.

Deaths are listed separately by sequence and period. The registry reports 1 death in each Period 1 sequence, and additional deaths in some later sequence-period entries. These figures are descriptive; the registry record does not establish that a death was caused by study treatment. Attribution and further clinical context are not reported in the registry record.

The listed serious adverse event terms include COVID-19, COVID-19 pneumonia, pneumonia, urinary tract infection, cystitis, and arthritis. Such event listings describe reports in the study record, not comparative causal effects. Interpreting safety requires attention to exposure duration, treatment sequence, event definitions, attribution, and the number of participants at risk in each period. The reported periods and sequences do not by themselves support a pooled treatment comparison.

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

The primary result describes the proportion meeting a specific Week 25 responder definition in the IgPro20 and placebo groups. The posted rates are 64.3% and 61.6%, respectively. The recalculated risk difference is 0.031, and its 95% confidence interval includes zero and values favoring either group. The result therefore does not demonstrate a clear difference between the groups on this endpoint.

That conclusion is not the same as showing that the treatments are equivalent or that no effect exists. The confidence interval remains compatible with a range of possible differences, and the registry does not report an equivalence or non-inferiority design or margin. A non-significant comparison cannot establish equivalence simply because it does not show a clear difference.

The result also does not answer every question about dermatomyositis. It concerns one composite responder definition at Week 25, including required earlier assessment and treatment-course conditions. It does not by itself establish effects on each component measure, longer-term outcomes, individual symptoms, safety in other populations, or outcomes not reported in the registry record.

The listed secondary outcomes broaden the trial’s assessment, but a complete pattern of results and the multiplicity strategy are not reported in the registry record. The serious adverse event listings are descriptive and do not establish treatment causation. Likewise, the terminated status is relevant context but does not explain why the trial ended or establish that termination altered the findings.

The most defensible interpretation is limited to the posted evidence: the Week 25 responder proportions were similar in the two arms, and uncertainty around the between-arm comparison is substantial. Neither the point estimate nor the absence of a clear statistical difference should be treated as a definitive statement about treatment efficacy or lack of efficacy.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate and its uncertainty should be read together. The primary arm percentages alone might suggest a small numerical separation, but the direct risk-difference interval is wide and crosses zero. The data therefore do not pin down the direction or size of the between-arm difference with much precision.

It also shows why analysis scale matters. The sponsor reports a logistic-regression odds ratio, while the unadjusted recalculation reports an absolute risk difference. Both are legitimate ways to summarize a binary outcome, but they answer different questions and cannot be compared as if they were the same quantity. Clear interpretation requires naming the measure, its reference value, and its interval.

The responder endpoint combines a multi-component score with visit timing and treatment-course conditions. That makes the definition more informative than a single score threshold alone, but it also means the overall responder proportion does not reveal which component determined each participant’s classification. Continuous scores and domain-specific outcomes can add context, provided their results and analysis methods are available.

Finally, the registry record raises standard questions about analysis populations, missing values, multiplicity, and trial status. It reports a modified intent-to-treat population and multiple imputation for a specified group of missing primary outcomes, but leaves important methodological details unreported. This is a useful reminder that statistical interpretation depends not only on the headline estimate, but also on how participants and outcomes were handled and how many comparisons were planned.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary population definition in the registry record is incomplete. It identifies screening and randomization to receive any amount of randomized investigational medicinal product, but the remaining eligibility statement is not reported. This limits assessment of the exact analysis population and its relationship to all randomized participants.

Missing primary-outcome values were addressed with multiple imputation for participants who discontinued due to military activities in Ukraine. The imputation model, variables, assumptions, and sensitivity analyses are not reported in the registry record. Handling of missing observations for other endpoints is also not reported. The impact of missing data on responder classification therefore cannot be fully assessed.

The registry gives the sponsor’s logistic-regression result but does not provide sufficient detail to reconstruct the model or determine whether covariates were included. It also does not report the full statistical analysis plan, multiplicity procedures, or a testing hierarchy. This limits interpretation of secondary findings and comparison of the sponsor’s model-based estimate with an unadjusted calculation.

The study is listed as terminated, while the reason for termination is not reported in the registry record. The record does not report the trial’s original sample-size justification, interim-analysis procedures, stopping rules, or complete masking procedures. Its brief description says double-blind, while the masking classification is quadruple; the roles masked are not reported.

Finally, the primary result concerns the specified Week 25 responder definition. The registry record does not report a clinically important threshold for the between-arm difference, so the estimate cannot be assessed against such a benchmark. These limitations constrain interpretation; they do not, by themselves, establish that the observed results are biased.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy, Safety, and Pharmacokinetics of IgPro20 in Adults With Dermatomyositis (DM) — NCT04044690.
• Registry record last updated 2025-12-09; status last verified 2025-11.
• Results first posted 2025-12-09.
• 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

The RECLAIIM study is a phase 3 randomized parallel-group trial of subcutaneous IgPro20 versus subcutaneous placebo in adults with dermatomyositis. The registry describes the study as placebo-controlled and double-blind, and classifies masking as quadruple. Its listed enrollment is 134, and its status is terminated.

The primary outcome is the Week 25 responder rate based on Total Improvement Score and additional visit and treatment-course conditions. The posted rates are 64.3% for IgPro20 and 61.6% for placebo. The unadjusted recalculated risk difference is 0.031, with a 95% confidence interval from -0.135 to 0.197. The sponsor reports a logistic-regression odds ratio of 1.13, with a 95% confidence interval from 0.551 to 2.309.

Both summaries leave substantial uncertainty about the primary comparison. The registry reports multiple imputation for specified missing primary outcomes, but the full analysis plan, detailed missing-data methods, multiplicity approach, and reason for termination are not reported in the registry record.