Five-year Actively Controlled Clinical Trial in New Onset Juvenile Dermatomyositis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Five-year Actively Controlled Clinical Trial in New Onset Juvenile Dermatomyositis (NCT00323960), a randomized phase 3 study. The primary outcome is Responder Status Defined as 20% Improvement in at Least 3 Core Set Variables With no More Than 1 of the Remaining Variables, (Muscle Strength Excluded), Worsened by > 30%..

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, randomized, parallel-group trial in juvenile dermatomyositis. Its official title calls it single-blind, while the registry masking entry is “NONE.” The record does not explain this difference, so the masking arrangement cannot be resolved from the registry information alone. The study status is completed, and the listed enrollment is 139.

Participants were assigned to one of three methylprednisolone-pulse and prednisone-based regimens: prednisone alone, prednisone plus cyclosporine A, or prednisone plus methotrexate. The registered arm counts are 47, 46, and 46, respectively. The posted primary endpoint is assessed at six months. The secondary outcomes include time to major therapeutic changes and time to prednisone, or equivalent, discontinuation; the major-therapeutic-changes outcome is reported over 60 months.

The registry lists a five-year project and gives the primary completion date as 2011-05-12. Details such as the randomization sequence, allocation concealment, site procedures, eligibility criteria, and the trial’s original sample-size rationale are not reported in the registry record. Although the title and summary describe a five-year study, the primary responder endpoint is a six-month measure; these answer different questions and should not be treated as interchangeable time points.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Comparison between group 2 (PDN+CSA) and 3 (PDN+MTX) combined versus group 1 (PDN)

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 Responder Status Defined as 20% Improvement in at Least 3 Core Set Variables With no More Than 1 of the Remaining Variables, (Muscle Strength Excluded), Worsened by > 30%., measured over 6 months.

The primary endpoint counts participants classified as responders at six months. Response requires 20% improvement in at least 3 core set variables and a restriction on worsening: no more than 1 of the remaining variables may have worsened by > 30%, with muscle strength excluded from that worsening rule. The core set described in the registry covers muscle strength, physician assessment of disease activity, disease activity assessment, parent or patient assessment of overall well-being, functional ability, and health-related quality of life.

A composite responder definition combines several domains into a single classification. In general, this can capture improvement across different aspects of a condition rather than relying on a single measurement. It can also make the result dependent on the exact thresholds, the number of domains that must improve, and how worsening is handled. Here, the primary outcome is a count of participants meeting the definition, rather than a mean change in one scale.

The primary comparison is described as the two add-on groups combined versus prednisone alone, while the posted arm counts and reported analyses also include all three groups. The registry does not provide a detailed account of how the combined primary comparison was constructed or how missing core-set measurements affected responder classification; those procedures are not reported in the registry record.

7. Results Posted in the Registry

• Group 2 (MPDN+PDN+CSA): 69.6% (32/46) versus 51.1% (24/47) on control; risk difference 18.5 percentage points (95% CI -1.0 to 38.0), risk ratio 1.36 (0.97–1.91); unadjusted two-proportion z-test p = 0.068.
• Group 3 (MPDN+PDN+MTX): 71.7% (33/46) versus 51.1% (24/47) on control; risk difference 20.7 percentage points (95% CI 1.3 to 40.0), risk ratio 1.40 (1.01–1.96); unadjusted two-proportion z-test p = 0.041.

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.

Time to Major Therapeutic Changes

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Group 2 (MPDN+PDN+CSA): 17.52 versus 30.52 (events per 1000 persons-time) on control; rate ratio 0.57 (95% CI 0.33–1.01, derived from the posted confidence limits); p ≈ 0.054.
  • Group 3 (MPDN+PDN+MTX): 13.92 versus 30.52 (events per 1000 persons-time) on control; rate ratio 0.46 (95% CI 0.25–0.83, derived from the posted confidence limits); p ≈ 0.010.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Group 2 (MPDN+PDN+CSA) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for Group 3 (MPDN+PDN+MTX) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The two secondary outcomes address different aspects of treatment course: time to major therapeutic changes and time to prednisone, or equivalent, discontinuation. For the reported major-therapeutic-changes outcome, the arm-level rate estimates are lower in both add-on groups than in the prednisone group. The sponsor also reports a Log Rank analysis. These results provide a longer-term perspective than the six-month responder endpoint, but they do not measure the same construct as the primary outcome.

The registry lists time to prednisone, or equivalent, discontinuation as a secondary outcome, but its result is not reported in the registry record. The registry indicates that two secondary outcomes were posted, while detailed results are available for the major-therapeutic-changes outcome. That leaves the broader secondary-outcome picture incomplete.

In general, secondary outcomes can help describe additional dimensions of a trial, but they are usually less decisive than a prespecified primary outcome, particularly when many outcomes or comparisons are considered. Multiple testing increases the chance that at least one result may appear notable by chance. The registry record does not report whether a multiplicity adjustment or hierarchy was planned, so unadjusted secondary results warrant less weight than a clearly specified primary analysis. They should be viewed as supportive or exploratory evidence rather than independent confirmation of the primary result.

The secondary findings are also subject to the limitations of the analysis details available in the registry. Procedures for handling censoring, missing observations, and analysis populations are not reported in the registry record. A time-to-event result depends on how event timing and follow-up are defined, so those details matter when relating it to the fixed six-month responder classification.

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

• Time to Major Therapeutic Changes
• Time to Prednisone, or Equivalent, Discontinuation

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods are most useful when each result is connected to the question it answers. The registry contains an overall three-group analysis for the primary endpoint, recalculated pairwise comparisons, and a time-to-event analysis for a secondary outcome. These analyses are not interchangeable, and the reported p-values should be interpreted alongside the endpoint definitions and confidence intervals.

What does the overall Chi-squared test assess?

The sponsor-reported primary analysis uses a Chi-squared test across all three groups, with p = 0.023. In general, a Chi-squared test assesses whether categorical outcome distributions differ across groups. Here, responder status is categorical: participants either meet the response definition or they do not. An overall test can indicate evidence of a difference somewhere among the groups, but it does not by itself identify which groups differ or quantify the size of each pairwise contrast. Pair-specific estimates require their own comparisons.

How do the recalculated risk differences work?

The posted recalculations use risk differences to compare each add-on group with prednisone alone. In general, a risk difference subtracts one group’s event proportion from the other group’s event proportion. Positive estimates in these comparisons indicate a higher observed responder proportion in the add-on arm than in the control arm, based on the direction used in the calculation. The estimates are unadjusted and derived from the posted summary counts. They are not adjusted for other participant characteristics or for multiple testing.

A confidence interval accompanies each recalculated risk difference. In general, the interval describes a range of values compatible with the data under the statistical model and its assumptions. A wide interval signals that the estimate is imprecise. Whether an interval includes zero is relevant to a risk difference because zero represents no difference on that scale, but this does not settle questions of clinical importance or multiplicity. The p-values attached to these recalculations are unadjusted.

What is different about the secondary time-to-event analysis?

Time-to-major-therapeutic-changes is recorded as events per 1000 persons-time over 60 months. The registry reports a Log Rank analysis and an associated relative risk. In general, time-to-event methods use information about when an event occurs and can account for differing observation times. A Log Rank test compares event-time patterns between groups; it does not simply compare the number of participants with an event at one fixed visit.

The registry also posts rates and recalculated rate ratios. In general, a rate compares the number of events with accumulated person-time, while a rate ratio compares rates between groups. Those measures are not the same as a participant-level risk difference. The registry’s reported Log Rank result and the simple recalculated rate comparisons therefore describe the outcome using different statistical summaries. Their estimates and p-values need not match because they answer different questions and may use different assumptions or methods.

For count outcomes, variation can exceed what a simple Poisson model expects; this is called over-dispersion. General statistical practice treats over-dispersion as important because standard errors and confidence intervals can be too narrow if the model assumes less variability than the data contain. The registry identifies the rate-based recalculations as Poisson-based, but details about model diagnostics or adjustments for over-dispersion are not reported in the registry record. The record also does not provide event-time curves or details of censoring procedures.

Why distinguish sponsor analyses from recalculations?

A recalculation from group-level summaries is a simple unadjusted analysis. It may not reproduce a sponsor’s analysis if that analysis used a different endpoint construction, analysis population, model, adjustment, or handling of missing observations. Those procedural details are not reported in the registry record. The primary sponsor analysis should therefore be kept distinct from the pairwise estimates recalculated from the posted counts; where the registry-derived comparison flags a discrepancy, the sponsor’s own analysis takes precedence.

More generally, statistical significance is not a measure of effect size, precision, or clinical value. A p-value describes how compatible the data are with a specified null model under the test assumptions. It does not give the probability that a treatment is effective, nor does it show whether an observed difference is large enough to matter clinically. Confidence intervals and the endpoint’s practical meaning are needed alongside the test result.

11. Confidence Intervals and Precision

The primary recalculated risk differences have confidence intervals that convey substantial uncertainty. For prednisone plus CSA versus prednisone alone, the estimate is 0.185 and the 95% confidence interval extends from -0.010 to 0.380. For prednisone plus MTX versus prednisone alone, the estimate is 0.207 and the 95% confidence interval extends from 0.013 to 0.4. These intervals show that the estimates are not precise enough to pin down a narrow range of possible differences.

In general, a confidence interval describes uncertainty in an estimate, conditional on the model and calculation used. It is not a guarantee that the true value falls within the particular interval, nor is it a range of individual participant outcomes. The interval for CSA includes zero, meaning the posted unadjusted data are compatible with both little or no difference and a positive difference on the risk-difference scale. The MTX interval is entirely positive, but remains broad. Neither interval addresses adjustment for multiple comparisons or unreported analysis choices.

The secondary rate estimates also have intervals. For example, the recalculated rate ratio for CSA has a 95% confidence interval from 0.326 to 1.011, while the MTX rate ratio interval is from 0.252 to 0.827. In general, rate-ratio intervals express uncertainty on a ratio scale, and their interpretation depends on which group is the numerator and which event definition is used. The sponsor’s separate Log Rank analysis reports a relative risk and its own interval. Differences between these estimates reflect distinct analysis approaches, not necessarily a contradiction in the underlying observations.

With the arm sizes reported in the registry, precision is limited, especially for outcomes with relatively few events. The registry does not report a clinical threshold for an important difference, so statistical uncertainty cannot be translated into a judgment about clinical importance.

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 illustrations estimate the number of participants per arm for the binary responder comparisons. For the time-to-major-therapeutic-changes outcome, the illustrations instead give the total number of events. These are planning illustrations based on the observed effects, not the trial’s original design calculations; the trial’s own sample-size justification is not reported in the registry record.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The 80% power column means the planned design would have an 80% chance of detecting that assumed effect under the planning assumptions if the effect were real. The 90% power column represents a higher detection probability under the same general setup and therefore requires more participants or events.

Smaller assumed effects require larger sample sizes because they are harder to distinguish from random variation. The planning figures are sensitive to the observed effect used as their starting point, and observed effects from a trial can be uncertain. They should be read as illustrations for future planning, not as a statement about the probability that this completed trial produced a significant result. This is not observed power.

When reading the figures, keep the unit in view: participants per arm applies to the binary endpoint illustrations, while total events applies to the time-to-event illustrations. The event-based quantities are not participant counts; one participant may contribute information differently under a time-to-event analysis. The original trial’s design assumptions, target power, and intended sample-size calculation are not reported in the registry record.

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 = 0.511; treatment proportion p₁ = 0.696; average p̄ = 0.603.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6919 = 1.3561.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6794 = 0.5718.
4. n = (1.3561 + 0.5718)² / (0.1850)² = 108.6, rounded up to 109 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 <- 0.51063829787234                          # control proportion
p1 <- 0.695652173913043                          # 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(323960)
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 = 109 (80% power), 145 (90% power)
 75% of observed effect: n per arm = 198 (80% power), 264 (90% power)
 50% of observed effect: n per arm = 452 (80% power), 604 (90% power)
power.prop.test: 108.6 
Simulated power at n = 109 per arm: 0.797 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a three-group Chi-squared test of responder status, with p = 0.023. That is the sponsor-reported result for the primary outcome. The separate pairwise risk differences and unadjusted p-values are recalculations from posted summary counts, not a replacement for that overall analysis.

The overall test asks whether there is evidence of a difference somewhere among the three groups. The recalculations instead compare the CSA group with prednisone alone and the MTX group with prednisone alone, one at a time. Because the questions and calculations differ, the results should not be expected to coincide numerically or to provide identical conclusions. The registry-derived analysis flags a discrepancy; in that circumstance the sponsor’s own analysis takes precedence.

The record does not include enough detail to determine precisely which analysis choices explain the difference, including any adjustments, the analysis population, or missing-data handling. Those details are not reported in the registry record. The safest reading is to retain the sponsor’s overall test as the reported trial analysis and treat the unadjusted recalculations as supplementary descriptions of the posted group counts, with their uncertainty and limitations made explicit.

15. Multiplicity, Missing Data and Analysis Populations

The record reports several comparisons and outcomes: a primary responder endpoint, two secondary outcomes, a sponsor-reported three-group test, and recalculated pairwise comparisons. Testing multiple hypotheses raises a general statistical issue: even if every null hypothesis were true, the chance of at least one apparently unusual result increases as the number of tests grows. This is why a prespecified testing hierarchy or multiplicity adjustment can matter.

Whether the trial used such a plan is not reported in the registry record. The recalculated pairwise p-values are explicitly unadjusted, so they should not be treated as multiplicity-controlled confirmatory tests. The record does not describe a sequence for testing the primary and secondary outcomes, nor does it state how the combined primary comparison was evaluated beyond identifying the population contrast. The sponsor’s reported analysis should be kept distinct from these recalculations.

Missing-data handling is another important uncertainty. The registry provides arm counts and outcome counts, but procedures for participants without a six-month assessment, incomplete core-set variables, or loss to follow-up are not reported in the registry record. The analysis population is also not reported in the registry record. It is therefore not possible to determine from the available record whether all randomized participants were included in each analysis or how incomplete observations affected response classification.

Likewise, the registry does not report whether analyses followed an intention-to-treat principle, used a per-protocol population, or applied imputation. These are not interchangeable approaches, and their implications depend on the reason data are missing and the assumptions used. The record also does not report interim analyses, stopping rules, or the trial’s original statistical analysis plan. No particular procedure should be inferred in their absence.

These gaps do not erase the reported results, but they limit how completely the analyses can be evaluated. In general, transparent reporting of multiplicity, missing-data methods, and analysis populations helps readers judge how much confidence to place in estimated effects and p-values.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: posterior reversible encephalopathy (2.2%), convulsion (2.2%), deep vein thrombosis (2.2%), appendicitis (2.2%), sepsis (2.2%).

The registry lists serious adverse events among 1 participant in the MPDN-plus-PDN group, 5 in the MPDN-plus-PDN-plus-CSA group, and 2 in the MPDN-plus-PDN-plus-MTX group. The corresponding numbers at risk are 47, 46, and 46. These are counts, not adjusted comparisons of safety between regimens. The registry also lists other adverse events affecting 29, 35, and 29 participants in the respective groups.

In general, adverse-event counts describe what was recorded during the study and do not by themselves establish that a treatment caused an event. They also do not indicate severity beyond the serious-event classification, duration, recurrence, or whether participants had more than one event. Those details are not reported in the registry record. The record does not report deaths; death counts are not reported in the registry record.

Several serious-event terms are each listed at 2.2%: posterior reversible encephalopathy, convulsion, deep vein thrombosis, appendicitis, sepsis, and paronychia. These entries should be read as listed terms, not as a complete assessment of comparative risk. The registry’s safety data alone cannot establish differences in causality or overall safety.

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

The registry results describe responder counts at six months, longer-term major-therapeutic-changes results, and adverse-event counts across three prednisone-based regimens. The sponsor’s reported primary analysis finds an overall difference across the three responder groups by its Chi-squared test. The separate unadjusted comparisons provide estimates for each add-on group versus prednisone alone, with confidence intervals that indicate uncertainty. These are statistical descriptions of the posted results, not medical advice.

The primary endpoint is a composite classification across several disease-related domains. Meeting that definition does not imply improvement in every measured domain, and the definition allows some worsening under its stated rule. The registry does not report how patients or clinicians should value a given change in the composite, nor does it provide a threshold for a clinically important between-group difference. Statistical evidence and clinical meaning are distinct considerations.

The results do not establish that any regimen works or does not work. They also do not establish that the regimens are equivalent, that any observed difference is caused by a particular component, or that the findings apply to populations beyond the trial’s described participants. Further, a six-month responder outcome cannot on its own answer every question about a five-year treatment course.

The secondary outcome and safety information add context but have limitations. The reported longer-term outcome uses time-to-event methods, while the primary outcome is a responder count at a fixed time. The discontinuation outcome’s results are not reported in the registry record. Adverse-event counts do not by themselves establish causality or comparative safety. Missing-data procedures, multiplicity handling, and analysis populations are not reported in the registry record, which constrains a full assessment of the evidence.

18. Why This Trial Matters Statistically

This trial is statistically notable for combining a three-arm randomized design with a composite responder endpoint and a longer-term event-based outcome. Those endpoints answer distinct questions: the primary measure classifies response at six months, while time to major therapeutic changes concerns events over a longer period. Keeping the outcome definitions separate is essential to avoid treating unlike measures as if they were one result.

The registry also illustrates the difference between an overall multi-group test and pairwise comparisons. The sponsor reports a single Chi-squared test across three groups, while the recalculations compare each add-on group with prednisone alone. The two approaches address related but nonidentical questions. A statistically notable overall test does not automatically identify which pairwise contrasts are responsible, and unadjusted pairwise tests raise multiplicity concerns.

Precision is equally important. The group counts and confidence intervals show why an estimate should not be reduced to a yes-or-no conclusion based on a p-value. The interval width communicates uncertainty, while the absence of a reported clinical-importance threshold limits interpretation of the magnitude.

Finally, this record makes clear how registry reporting affects statistical appraisal. Important details about the original sample-size rationale, missing data, multiplicity, and analysis populations are not reported in the registry record. Readers can interpret the posted estimates, but should distinguish documented analyses from procedures that cannot be established from the record.

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.

Several limitations are specific to the information recorded for this trial. The official title describes the study as single-blind, but the registry masking entry is “NONE”; the record does not explain the difference. The precise masking arrangement is therefore unclear from the registry record.

The trial’s original sample-size justification and statistical analysis plan are not reported in the registry record. The posted planning illustrations are based on observed effects and should not be confused with the trial’s original design. Details on randomization implementation, allocation concealment, eligibility criteria, and the analysis population are also not reported in the registry record.

For the primary outcome, the registry does not provide procedures for incomplete core-set measurements or missing six-month assessments. It also does not report whether multiplicity was addressed across comparisons and outcomes. These omissions limit assessment of the recalculated unadjusted pairwise results and of how they relate to the sponsor’s overall analysis.

Although the record names time to prednisone discontinuation as a secondary outcome, its results are not reported in the registry record. Details about censoring and event definitions for the reported time-to-major-therapeutic-changes analysis are not reported in the registry record. The safety listing also lacks detail on event timing, recurrence, and causality. These limits do not negate the posted results, but they narrow what can be concluded from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Five-year Actively Controlled Clinical Trial in New Onset Juvenile Dermatomyositis — NCT00323960.
• Registry record last updated 2023-03-28; status last verified 2023-03.
• Results first posted 2021-03-16.
• 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 registry describes NCT00323960, a completed Phase 3 randomized parallel-group trial in juvenile dermatomyositis with enrollment of 139. Participants received methylprednisolone pulse and prednisone-based treatment alone, with cyclosporine A, or with methotrexate. The primary endpoint was responder status at six months, using a multi-domain improvement and worsening definition.

The sponsor reports an overall three-group Chi-squared analysis with p = 0.023. Recalculated pairwise comparisons are unadjusted and should be kept distinct from that sponsor analysis; where a discrepancy is flagged, the sponsor’s own analysis takes precedence. The registry also reports a longer-term major-therapeutic-changes outcome and adverse-event counts. Results for prednisone discontinuation, detailed missing-data methods, multiplicity procedures, and the original sample-size justification are not reported in the registry record.