A Study to Evaluate the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of Satralizumab in Participants With Thyroid Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of Satralizumab in Participants With Thyroid Eye Disease (NCT06106828), a randomized phase 3 study. The primary outcome is Percentage of Participants in the Active TED Population Who Achieved ≥ 2 Millimeters (mm) Reduction in Proptosis From Baseline at Week 24 in the Study Eye.

2. Clinical Question

3. Trial Design

The registry describes NCT06106828 as a Phase III, randomized, double-masked, placebo-controlled, multicenter, parallel-group study of satralizumab in participants with moderate-to-severe thyroid eye disease. The listed masking level is quadruple. The study is marked completed, with registry enrollment of 127. Its stated purpose was to assess efficacy, safety, pharmacokinetics, and pharmacodynamics of subcutaneous satralizumab, a recombinant, humanized anti-interleukin-6 receptor monoclonal antibody.

Part I compared satralizumab with placebo, administered every 4 weeks. In Part II, both groups were to receive treatment individualized according to proptosis response. The primary outcome is measured at Week 24 and is described for the active TED population. The efficacy summaries report 48 participants in the satralizumab group and 49 in the placebo group for this outcome. The overall-population proptosis outcomes use different reported group denominators. Those outcome-specific populations and denominators should not be treated as interchangeable.

The registry lists 41 outcome measures and 17 analyses. It reports several secondary outcome domains, including proptosis response and change, diplopia, pain, and visual functioning. The specific numerical results discussed in the registry record are not equally detailed across these domains. The original sample-size rationale and other design details, including whether the trial used interim analyses, are not reported in the registry record. The statistical analysis plan beyond the methods named in the posted analyses is also 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: Participants were randomized in a 1:1 ratio to receive either subcutaneous (SC) satralizumab or a matching placebo in Part I (Weeks 1-24). After Part I analysis, proptosis non-responders from either arm received satralizumab, and proptosis responders were re-randomized in a 1:1 ratio to receive either satralizumab or matching placebo in Part II. The data for Part II will be presented 1 year after the study completion date.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Part I FAS included all randomized participants, with participants grouped according to the treatment they were assigned at baseline.

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: Part I Full Analysis Set (FAS) included all randomized participants, with participants grouped according to the treatment they were assigned at baseline.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants in the Active TED Population Who Achieved ≥ 2 Millimeters (mm) Reduction in Proptosis From Baseline at Week 24 in the Study Eye, measured over At Week 24.

The primary endpoint is the percentage of participants in the active TED population who achieved at least a 2 mm reduction in proptosis from baseline to Week 24 in the study eye. To count as a response, a participant also had to avoid a corresponding deterioration of at least 2 mm in the fellow eye. Proptosis is the measure of how far the eye projects; the endpoint therefore focuses on a specified change in eye prominence rather than on a broader composite of symptoms or function.

A threshold outcome can be clinically interpretable because it describes the proportion reaching a prespecified degree of change. It also discards information about the size of changes that fall short of the threshold and about differences among participants who do respond. A participant just meeting the threshold and one with a larger reduction are both counted as responders. The endpoint is therefore complemented by the continuous secondary outcome measuring change in proptosis.

The primary outcome’s definition includes both the study eye and a safeguard against a specified worsening in the fellow eye. The registry says percentages were rounded. It identifies the Part I FAS as including all randomized participants grouped according to baseline assignment, while the endpoint itself is defined for the active TED population. The detailed rules for handling missing Week 24 measurements are not reported in the registry record.

7. Results Posted in the Registry

• Part I: Satralizumab: 52.1% (25/48) versus 22.4% (11/49) on control; risk difference 29.6 percentage points (95% CI 11.3 to 48.0), risk ratio 2.32 (1.29–4.17); unadjusted two-proportion z-test p = 0.003.

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 in the Overall Population Who Achieved ≥ 2 mm Reduction in Proptosis From Baseline at Week 24 in the Study Eye

• 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:
  • Part I: Satralizumab: 46.9% (30/64) versus 22.2% (14/63) on control; risk difference 24.7 percentage points (95% CI 8.7 to 40.6), risk ratio 2.11 (1.24–3.59); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Part I: Satralizumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Proptosis at Week 24 in Active TED Population for Study Eye

• 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:
  • Part I: Satralizumab: mean -1.97 versus -0.96 on control; difference -1.01 (95% CI -1.66 to -0.36), standardized effect d = -0.62; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Part I: Satralizumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Proptosis at Week 24 in Overall Population for Study Eye

• 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:
  • Part I: Satralizumab: mean -1.54 versus -0.99 on control; difference -0.55 (95% CI -1.15 to 0.05), standardized effect d = -0.32; z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part I: Satralizumab and the control. The interval gives the range of effects that remain compatible with the data.

The reported secondary proptosis outcomes broadly point in the same direction for the binary response measures: the posted satralizumab group response percentage exceeds the placebo group percentage in both the active TED and overall populations. The active-population continuous proptosis result also has a sponsor-reported adjusted mean difference below zero, whereas the overall-population continuous result has a confidence interval that includes zero. These measures address related but non-identical questions, and their estimates should not be collapsed into one summary claim.

The secondary outcomes extend the primary question by examining proptosis in the overall population and by measuring change as a continuous quantity. The registry also lists outcomes concerning diplopia, pain, and visual functioning. Their numerical findings are not reported in the registry record, so no direction or size of effect for those outcomes can be stated. The registry lists 40 secondary outcomes; the available result summaries in the record are not a basis for asserting the same pattern across all secondary outcomes.

Secondary outcomes are usually interpreted with more caution than the primary endpoint. A trial can assess many outcomes, populations, time points, and analysis approaches. When many hypotheses are tested, the chance of at least one apparently notable result can increase unless multiplicity is addressed. The registry does not report whether or how the secondary analyses were adjusted for multiplicity. Their p-values should therefore be viewed as individual, unadjusted evidence unless the registry explicitly identifies otherwise.

Secondary outcomes can help assess consistency and illuminate different dimensions of the disease, but they do not supersede the primary endpoint. The primary result concerns a particular response threshold, population, and time point. Secondary findings add context within their own definitions and do not establish that every measured symptom or functional outcome changed in the same way.

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

• Percentage of Participants in the Overall Population Who Achieved ≥ 2 mm Reduction in Proptosis From Baseline at Week 24 in the Study Eye
• Change From Baseline in Proptosis at Week 24 in Active TED Population for Study Eye
• Change From Baseline in Proptosis at Week 24 in Overall Population for Study Eye
• Percentage of Participants in Active TED Population Achieving ≥ 1 Grade Reduction/Improvement in Diplopia at Week 24
• Percentage of Participants in the Overall Population Achieving ≥ 1 Grade Reduction/Improvement in Diplopia at Week 24
• Percentage of Participants in Active TED Population Achieving Absence of Motility-induced Pain at Week 24
• Percentage of Participants in Active TED Population Achieving Absence of Spontaneous Pain at Week 24
• Percentage of Participants in Active TED Population With a ≥ 6-point Improvement in the Visual Functioning Subscale of the Graves' Ophthalmopathy Quality-of-life (GO-QoL) From Baseline at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary endpoint is binary for each participant: the participant either meets the defined response criterion at Week 24 or does not. The group-level percentage estimates the frequency of that response in each assigned group. A risk difference compares those two proportions by subtraction; on the proportion scale, zero denotes no difference. The re-calculated risk difference and its interval are reported on that proportion scale. The sponsor reports its result as a difference in response rates expressed in percentage points.

Binary endpoints are useful when the question concerns the proportion crossing a meaningful threshold. Their interpretation depends on the threshold definition, the population included, and the way missing outcome data are handled. They also compress variation: response status does not convey how far a responder exceeded the threshold or how close a non-responder came to it.

Why are there two kinds of analysis?

The simple re-calculation uses the posted group counts and denominators to make an unadjusted comparison. It is useful as a check on the direction and approximate scale of the group contrast using summary information. It does not reproduce an analysis that adjusts or stratifies for design factors unless those features are explicitly built into the calculation. The registry identifies the sponsor’s primary comparison as Mantel-Haenszel, a method that can combine comparisons across strata. The stratification factors and the full implementation details are not reported in the registry record.

The registry identifies the continuous change outcomes as analyzed using MMRM, or a mixed model for repeated measures. In general, this class of model uses measurements taken over time and accounts for their correlation within a participant. It can estimate adjusted group differences while using repeated observations, subject to the model specification and assumptions. The registry gives the Week 24 adjusted mean differences, but the full covariance structure, covariates, missing-data assumptions, and model specification are not reported in the registry record. A simple comparison of posted means is therefore a useful descriptive check, not a reproduction of the model.

How should a confidence interval be understood?

A confidence interval describes statistical uncertainty around an estimate under the analysis method and its assumptions. In repeated use, a confidence-interval procedure with its stated confidence level would cover the target value at that rate. For a difference, an interval that includes zero is compatible with no difference under that procedure; an interval that excludes zero indicates the data are less compatible with that null value. The interval does not state the probability that the true effect lies within the particular reported bounds, and it does not account for every possible source of bias or uncertainty.

For a proportion difference, the interval’s endpoints use the same scale as the estimate. For a mean difference, the endpoints are expressed in the outcome’s units, here millimeters. Width matters: a narrower interval indicates greater statistical precision under the analysis, while a wider one allows a broader range of effects. Precision does not establish that an effect is important to patients.

What does over-dispersion mean in general?

For a binary outcome, a simple model may assume that the observed variability follows the model’s specified distribution. Over-dispersion means the data vary more than that model expects. When present and unaccounted for, it can make standard errors too small and intervals or tests overly optimistic. The registry information does not identify over-dispersion as an issue or describe a specific adjustment for it; this is a general statistical consideration, not a finding about this trial.

How should p-values be read?

A p-value measures how incompatible the observed data, or more extreme data, are with a specified null hypothesis under the model used. It is not the probability that the null hypothesis is true, nor does it measure effect size or clinical importance. The sponsor reports p-values for the stated analyses. The re-calculated p-values are unadjusted and arise from simpler calculations. Small differences between the two do not necessarily indicate a mistake because the methods and assumptions differ.

Why do the binary and continuous outcomes differ?

The response endpoint counts participants who cross a fixed threshold. The continuous endpoint retains the magnitude of each participant’s measured change and compares group averages. A group can have a different fraction crossing a threshold without a correspondingly strong difference in the mean, or the reverse, because the outcomes summarize the data differently. Here, the registry reports both types of proptosis outcome, with separate populations for active TED and the overall population. They are related measures, but neither is a direct substitute for the other.

The posted sponsor analyses are the Mantel-Haenszel comparison for the binary response and MMRM analyses for continuous change. The registry does not report a complete statistical analysis plan, all model details, or the rationale behind every analysis choice. Interpretation should therefore distinguish the methods actually named in the record from any broader assumptions that cannot be verified from it.

11. Confidence Intervals and Precision

The primary sponsor estimate is a 28.9-percentage-point difference in response rates, with a 95.03% confidence interval from 11.5 to 46.2. The interval lies above zero, indicating that the reported analysis is inconsistent with equal response rates under the model and confidence procedure used. Its width also shows that the estimate is not exact: the data are compatible with a range of positive differences. The point estimate should not be treated as the only plausible value.

The simple re-calculation gives a risk difference of 0.296, with an interval from 0.113 to 0.480. Because this is on the proportion scale, these values are not written in the same units as the sponsor’s percentage-point result. The estimates use different analytical approaches, so the intervals should be interpreted within their respective methods rather than combined or treated as interchangeable.

For the active-population continuous outcome, the sponsor’s adjusted mean difference is -1.02 mm, with a 95.03% confidence interval from -1.67 to -0.36. This interval is entirely below zero on the change-from-baseline scale. For the overall-population continuous outcome, the adjusted mean difference is -0.55 mm and its interval runs from -1.14 to 0.03; this interval includes zero. These intervals describe statistical precision for different populations and outcome definitions, and should not be used as though they estimate the same quantity.

Confidence intervals reflect sampling uncertainty under the stated analysis, not uncertainty from every possible source. They do not correct for unreported design features, missing-data assumptions, measurement issues, or multiple testing. The registry does not report the full analysis details needed to assess all such influences.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effects, not the trial’s original design calculations. For these binary and continuous comparisons, the listed figures are participants per arm, not total participants or total events. The 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 trial’s own original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation indicates would give an 80% chance of rejecting the null hypothesis if the assumed effect and planning conditions held. The 90% power column uses a higher target chance of detecting that assumed effect, so it generally requires more participants per arm. These are design-planning probabilities under assumptions, not probabilities that the reported trial result is true. The figures are not observed power.

Rows that plan for 75% or 50% of the observed effect use progressively smaller assumed effects. Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants per arm. This relationship is a general property of statistical design: other things held constant, detecting a smaller difference typically requires a larger sample.

The planning values should be read as conditional illustrations, not recommendations or evidence that the study was adequately or inadequately sized. They do not account for every practical feature that may affect a real trial, including outcome availability, model adjustment, multiplicity, or departures from the assumptions. The record does not report the trial’s own sample-size justification, so the illustrations cannot establish what assumptions guided the original enrollment target.

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 = 0.224; treatment proportion p₁ = 0.521; average p̄ = 0.373.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6838 = 1.3402.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6509 = 0.5478.
4. n = (1.3402 + 0.5478)² / (0.2963)² = 40.6, rounded up to 41 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 <- 0.224489795918367                          # control proportion
p1 <- 0.520833333333333                          # 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(6106828)
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 = 41 (80% power), 54 (90% power)
 75% of observed effect: n per arm = 70 (80% power), 93 (90% power)
 50% of observed effect: n per arm = 149 (80% power), 199 (90% power)
power.prop.test: 40.6 
Simulated power at n = 41 per arm: 0.817 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s sponsor analysis for the primary endpoint is a Mantel-Haenszel comparison of response rates. It reports a difference of 28.9 percentage points, a 95.03% confidence interval from 11.5 to 46.2, and p = 0.001. This is the analysis identified in the record as the superiority result. Its confidence interval excludes zero.

The separate recalculation uses the posted summary counts in a simple unadjusted comparison. It reports a risk difference of 0.296, an interval from 0.113 to 0.480, and an unadjusted p-value of 0.003. These results are broadly consistent in direction with the sponsor analysis, but the estimates and uncertainty measures do not match exactly. The two methods are not equivalent: one is the registry’s Mantel-Haenszel analysis, while the other is a re-calculation from summary statistics without that adjustment.

The record does not flag a discrepancy between the recalculation and sponsor analysis. The recalculation is best understood as a transparent statistical cross-check, not as a replacement for the trial’s reported analysis. The registry does not provide enough detail about stratification or the complete analysis plan to reproduce the sponsor result exactly.

For continuous outcomes, the same distinction applies. The sponsor reports MMRM adjusted mean differences, while the recalculations are simple unadjusted estimates from the posted summaries. Their similarity or difference should be assessed with awareness that adjustment, repeated-measures modeling, and analysis assumptions can affect the estimate and its uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint alongside many secondary outcomes and analyses. Testing multiple outcomes creates a multiplicity problem: even when no true group differences exist, repeated testing can make one or more nominally positive findings more likely. Common approaches include prespecifying a hierarchy, adjusting significance thresholds, or controlling a family-wise or false-discovery error rate. The registry record does not report whether a multiplicity procedure was used, which outcomes were included in any testing family, or whether the secondary p-values were adjusted. Consequently, the primary and secondary results should not be treated as if every reported test had the same confirmatory status.

The record describes the Part I FAS as including all randomized participants grouped according to baseline assignment. This is an assignment-based population description. The primary outcome is specifically defined for the active TED population, so the population wording and reported outcome denominators matter when interpreting the result. The registry does not report all details needed to establish how the active TED subset was defined for analysis or how participants with missing Week 24 measurements were handled.

Missing outcome data can affect both response percentages and continuous estimates. In general, analyses may use different assumptions about whether missingness is related to observed or unobserved outcomes. Sensitivity analyses can help assess how robust results are to those assumptions. The registry does not report the missing-data method, the amount or pattern of missing primary outcome data, or sensitivity analyses for the primary endpoint.

The listed sponsor methods include Mantel-Haenszel analysis for the binary primary endpoint and MMRM for continuous outcomes. The record does not report the full model specifications, covariate choices, stratification details, or all analysis-set rules. These omissions limit independent reconstruction and make it difficult to evaluate some assumptions. They do not by themselves show that the analyses were inappropriate; they identify information 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: syncope (3.1%), endocrine ophthalmopathy (1.6%), cellulitis gangrenous (1.6%), arthropod bite (1.6%), rotator cuff syndrome (1.6%).

The registry’s Part I safety summaries report serious adverse events among 64 participants at risk in the satralizumab group and 62 at risk in the placebo group. Serious adverse events affected 2 and 3 participants, respectively. Deaths are reported as 0 in each group. The listed denominators are safety-summary denominators and differ from the primary active-population efficacy denominators; they should not be substituted for one another.

The registry also lists serious adverse event terms with reported percentages: syncope at 3.1%, endocrine ophthalmopathy at 1.6%, cellulitis gangrenous at 1.6%, arthropod bite at 1.6%, rotator cuff syndrome at 1.6%, and ankle fracture at 1.6%. These are registry-listed terms, not a complete description of every possible adverse event. The record excerpt does not supply enough detail to infer comparative risk for each term, its causal relationship to treatment, or the timing and duration of events.

Safety counts describe what was reported in the trial and should be interpreted in light of the study’s size, duration, event definitions, and ascertainment. The registry record does not provide enough information to assess all of those features. A small number of reported events cannot rule out uncommon or longer-term risks, and the counts alone do not establish that an event was caused by the assigned treatment.

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

The primary result describes a higher Week 24 response percentage in the satralizumab-assigned group than in the placebo-assigned group for the specified active TED population and proptosis threshold. The sponsor’s reported comparison estimates the difference in response rates and gives a confidence interval that excludes zero. This is evidence about a group-level contrast in this trial under the reported analysis, not a guarantee of response for any particular participant.

The endpoint has a specific scope: it measures a reduction of at least 2 mm in the study eye while requiring no corresponding deterioration of at least 2 mm in the fellow eye. It does not by itself describe all aspects of thyroid eye disease, patient experience, visual function, long-term outcomes, or safety. The registry lists related outcomes, but numerical results for several of those domains are not reported in the registry record. The result therefore cannot be generalized to every outcome simply because it is positive for the primary endpoint.

The primary estimate is not the only relevant summary. The continuous proptosis outcomes offer a different view of change, and the overall-population result has a confidence interval that includes zero. These differences are not inherently contradictory: threshold response and average change answer different statistical questions and use different populations. The registry’s reported analyses should be read with their outcome definitions and populations attached.

Statistical evidence does not alone establish clinical importance. The record does not provide a threshold for a clinically meaningful between-group difference, nor does it report all details needed to judge whether the endpoint captures outcomes that matter most to participants. It also does not report the full missing-data or multiplicity procedures. Thus the posted results support a precise statement about the reported Week 24 comparison, while leaving broader questions about durability, all symptom domains, and generalizability unresolved.

No treatment recommendation follows from these statistical summaries. They describe trial results and their uncertainty; clinical decisions require broader evidence and individual context that are not addressed by the registry analysis.

18. Why This Trial Matters Statistically

This trial illustrates why the definition of an endpoint matters as much as the headline percentage. The primary outcome is not simply any improvement in proptosis: it requires a threshold reduction in the study eye and restricts worsening in the fellow eye. That makes the response percentage interpretable against a clear rule, while also making the result dependent on that rule and its measurement.

It also demonstrates the value of distinguishing a response proportion from a continuous outcome. A threshold outcome answers how many participants cross a specified boundary; a mean-change outcome summarizes the magnitude of change across a group. The registry reports both forms, and their results are not identical in statistical certainty across the active and overall populations. This is a useful reminder that a positive result on one endpoint does not imply uniform evidence across all related measures.

The record further illustrates the difference between a sponsor’s analysis and a simple recalculation. A summary-statistic check can clarify the scale and direction of a contrast, but it does not reproduce stratified or repeated-measures analyses. Transparent separation of the methods makes estimates easier to interpret without implying that the simpler calculation is the definitive trial analysis.

Finally, the trial shows why statistical significance, precision, multiplicity, and reporting completeness must be considered together. Confidence intervals convey a range of estimates compatible with an analysis, while missing information about the full analysis plan and secondary testing limits how far conclusions can extend. Careful reading keeps the conclusion attached to the population, outcome, time point, and method actually reported.

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 outcome is reported at Week 24, and the registry record does not provide a longer-term estimate for this response endpoint. Part II involves proptosis response-based individualized treatment, so the Part I Week 24 comparison should not be treated as an estimate of a continued fixed-treatment contrast beyond that period. Details of the Part II results are not reported in the registry record.

The primary outcome is restricted to the active TED population, while some secondary outcomes use the overall population. The registry describes the active population broadly as participants with active disease but does not provide the full operational definition in the outcome summary. Population-specific estimates are not interchangeable, and differences between active and overall results may reflect the differing populations as well as the outcome measure.

The registry gives rounded percentages and outcome-specific denominators. It does not provide full participant-level data, so the posted summaries cannot support independent checks of covariate balance, missingness patterns, or alternate model specifications. The trial’s original sample-size assumptions and justification are not reported in the registry record; planning illustrations based on observed effects do not fill that gap.

The registry names Mantel-Haenszel and MMRM methods but does not provide the complete analysis plan, model specifications, missing-data approach, or multiplicity procedure. These reporting gaps limit reconstruction and assessment of robustness. The listed safety data are also summaries: they do not establish event causality, describe all event timing, or resolve the possibility of uncommon events. These limitations constrain interpretation of the registry record without determining whether the trial itself was conducted appropriately.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of Satralizumab in Participants With Thyroid Eye Disease — NCT06106828.
• Registry record last updated 2026-08-12; status last verified 2026-07.
• Results first posted 2026-08-12.
• 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

NCT06106828 is a completed Phase III randomized, double-masked, placebo-controlled, multicenter study of satralizumab in moderate-to-severe thyroid eye disease. Part I compared subcutaneous satralizumab every 4 weeks with placebo every 4 weeks; Part II used proptosis response-based individualized treatment. Registry enrollment was 127.

The primary Week 24 endpoint was the percentage of participants in the active TED population achieving at least a 2 mm reduction in proptosis in the study eye without a corresponding deterioration in the fellow eye. The sponsor reports a 28.9-percentage-point difference in response rates, with a 95.03% confidence interval from 11.5 to 46.2 and p = 0.001. Simple recalculations are unadjusted and are distinct from the sponsor’s named analyses. Secondary proptosis outcomes provide additional, non-identical summaries; the registry record does not report all details needed to assess multiplicity, missing-data handling, or the full analysis plan.