A Safety, Tolerability, and Efficacy Study of Veligrotug (VRDN 001) in Participants With Thyroid Eye Disease (TED): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety, Tolerability, and Efficacy Study of Veligrotug (VRDN 001) in Participants With Thyroid Eye Disease (TED) (NCT05176639), a randomized phase 3 study. The primary outcome is Proptosis Responder Rate (PRR) in the Study Eye As Measured by Exophthalmometer.

2. Clinical Question

The clinical question is specific to a measured change in eye protrusion over the stated assessment period. It is not a general measure of every aspect of TED, and the primary endpoint does not by itself describe symptoms, quality of life, longer-term outcomes, or the full safety profile. The registry record also identifies safety, tolerability, pharmacokinetic, and pharmacodynamic objectives, but the primary efficacy comparison is the proportion meeting the responder definition.

3. Trial Design

NCT05176639 is a completed phase 3 randomized, triple-masked, parallel-group trial sponsored by Viridian Therapeutics, Inc. The registry record lists an enrollment of 113 and identifies thyroid eye disease as the condition under study. The trial began on 2022-11-16, with primary completion on 2024-07-15.

Participants were allocated to veligrotug or matched placebo. The veligrotug regimen was 10 mg/kg by intravenous infusion every 3 weeks for 12 weeks; placebo was administered on the same schedule. The registry describes veligrotug as a monoclonal antibody that inhibits IGF-1R activity. Its summary states that inhibition may help reduce inflammation and associated tissue swelling in TED. That biological rationale is not itself evidence of a clinical effect; the randomized comparison of outcomes is the relevant evidence for the trial question.

The primary endpoint was the proptosis responder rate in the study eye, measured by exophthalmometer from baseline to Week 15. The primary analysis population was the mITT population, defined in the registry as randomized participants who received at least 1 dose of study drug. The registry says that results were reported for participants and that the Ns represent participants analyzed regardless of which eye was evaluated.

The registry lists 10 outcome measures and 9 posted secondary outcomes. These include other proptosis measurements, clinical activity, overall response, and diplopia outcomes. The record names safety, tolerability, pharmacokinetic, and pharmacodynamic objectives in its summary. Further details about the trial’s original sample-size justification, planned interim analyses, or full statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Ocular assessments were performed in both eyes at baseline. Study eye was the most proptotic eye by exophthalmometer at baseline. If both eyes were equally proptotic, then the eye with the worse visual acuity (VA) was designated as the study eye. If proptosis and VA were equal in both eyes, then the right eye was designated as the study eye.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT population included all randomized participants who received at least 1 dose of study drug. As prespecified, data were collected and reported for the participants. Therefore, the 'Ns' reported below = number of participants analyzed regardless of which eye was evaluated.

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: Modified Intent-to-Treat (mITT) population included all randomized participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Proptosis Responder Rate (PRR) in the Study Eye As Measured by Exophthalmometer, measured over Baseline to Week 15.

The primary endpoint is the percentage of participants classified as proptosis responders in the study eye from baseline to Week 15. The study used an exophthalmometer to measure proptosis. A responder was defined as having a reduction of at least 2 mm from baseline in the study eye, without a corresponding increase of at least 2 mm in the fellow eye. This definition combines improvement in the study eye with a condition intended to rule out a substantial worsening in the other eye.

A responder rate turns a measurement into a clinically interpretable event: whether or not each participant met the prespecified threshold. Comparing the proportions in the randomized groups estimates how often the defined response was observed under each assigned treatment condition. The percentage does not show the size of every participant’s change, and two people who both meet the threshold may have had different magnitudes of change. The separately listed continuous proptosis outcomes address change in millimeters rather than the binary responder classification.

The endpoint is useful because it specifies a measurable threshold, an eye, an instrument, and an assessment period. It should nevertheless be interpreted as one outcome among the trial’s safety and efficacy measures, not as a complete account of TED. Missing primary endpoint data were imputed using the Multiple Imputation method. Details beyond that description, including the imputation model, are not reported in the registry record.

7. Results Posted in the Registry

• Veligrotug: 69.3% (52/75) versus 5.3% (2/38) on control; risk difference 64.1 percentage points (95% CI 51.4 to 76.7), risk ratio 13.17 (3.39–51.19); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in Proptosis in the Study Eye As Measured by Exophthalmometer

• 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:
  • Veligrotug: mean -2.90 versus -0.48 on control; difference -2.42 (95% CI -3.01 to -1.83), standardized effect d = -1.58; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Veligrotug than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

PRR in the Most Proptotic Eye As Measured by Magnetic Resonance Imaging (MRI)/Computed Tomography (CT)

• 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:
  • Veligrotug: 70.7% (53/75) versus 10.5% (4/38) on control; risk difference 60.1 percentage points (95% CI 45.9 to 74.3), risk ratio 6.71 (2.63–17.16); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Veligrotug than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Proptosis in the Most Proptotic Eye As Measured by MRI/CT

• 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:
  • Veligrotug: mean -2.96 versus -0.58 on control; difference -2.38 (95% CI -3.03 to -1.73), standardized effect d = -1.44; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Veligrotug than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover complementary aspects of TED and proptosis: responder status measured with MRI or CT, change in proptosis in the study eye, change in the most proptotic eye, clinical activity, overall response, and diplopia. Among the secondary results with numerical estimates and recalculated comparisons in the registry record, the proptosis measures show a pattern consistent with the primary endpoint: the veligrotug arm has a larger observed improvement or responder proportion than placebo. These outcomes provide related, but not identical, views of the clinical question because they differ in measurement method, eye definition, or whether the result is a threshold response or a continuous change.

The primary endpoint remains the central efficacy result. Secondary measures can support a broader interpretation when they point in a similar direction, but they do not independently confirm the primary result simply because they are related. The registry lists additional secondary outcomes, including clinical activity and diplopia response or resolution; numerical estimates for those outcomes are not reported in the registry record, so their results cannot be characterized.

Unadjusted secondary comparisons carry less inferential weight when multiple outcomes are examined. In general, the chance of at least one apparently notable finding can rise as the number of separate tests increases. A prespecified testing sequence or multiplicity adjustment can address this concern, but the multiplicity plan is not reported in the registry record. The secondary findings should therefore be treated as supportive and exploratory in interpretation, not as a collection of equally definitive conclusions. Agreement across related proptosis measures adds context, while differences in endpoint definitions and missing reporting limit how far that pattern can be generalized.

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

• Change From Baseline in Proptosis in the Study Eye As Measured by Exophthalmometer
• PRR in the Most Proptotic Eye As Measured by Magnetic Resonance Imaging (MRI)/Computed Tomography (CT)
• Change From Baseline in Proptosis in the Most Proptotic Eye As Measured by MRI/CT
• Change From Baseline in CAS in the Study Eye
• Overall Responder Rate (ORR) Comprising of PRR and Clinical Activity Responder Rate in the Study Eye
• Clinical Activity Responder Rate in the Study Eye
• Diplopia Responder Rate
• Diplopia Resolution Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary result is a binary outcome: each analyzed participant either met the responder definition or did not. For a binary outcome, the arm-level percentage describes the proportion with the event. A risk difference compares those proportions by subtraction, but the recalculated estimate is quoted as posted rather than recomputed. In general, a risk difference is an absolute contrast, while a risk ratio compares proportions multiplicatively. The recalculated comparison also includes relative measures, but interpretation emphasizes the absolute risk difference because it directly describes the difference in response probability.

What does the confidence interval describe?

A confidence interval describes uncertainty in an estimate under the method used to construct it. In repeated use of the same procedure under its assumptions, intervals would cover the target quantity at the stated confidence level at the stated rate. For this primary outcome, the recalculated interval is 0.514 to 0.767 for the risk difference. It communicates both the estimated contrast and its sampling uncertainty; it does not account automatically for every possible source of bias, model misspecification, or uncertainty about generalizing beyond the trial.

Why are the unadjusted calculation and registry model distinct?

The recalculation is an unadjusted comparison based on the posted arm summaries. The registry reports a logistic-regression analysis with risk difference as the reported measure. Regression methods can account for covariates or other modeling features when specified, whereas a simple comparison of summary proportions does not. The covariates and detailed model specification are not reported in the registry record. Accordingly, the two estimates should be identified by their analysis approach rather than treated as interchangeable. The registry reports its analysis with a 95% confidence interval and p-value; the recalculated result has its own unadjusted interval and p-value.

What does the p-value add?

A p-value describes how incompatible the observed data, or data more extreme, would be with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary recalculation reports p <0.001, while the registry analysis reports p < 0.001. Both values are tied to their respective methods. They do not replace the effect estimate, its interval, or consideration of study design and outcome relevance.

How do continuous outcomes differ?

Secondary continuous outcomes describe changes in proptosis in millimeters using least-squares means and standard errors. A mean difference summarizes a contrast in average change rather than the proportion crossing a threshold. The posted recalculations for these outcomes use approximate standard deviations derived from the reported standard errors. Such recalculations are summary-statistic illustrations, not the registry’s model-based results; no sponsor-reported analyses are listed for those outcomes in the record. In general, standard errors describe the precision of an estimated mean, while standard deviations describe variation among individual observations. They are related, but they are not the same quantity.

Why can variation affect a binary comparison?

For binary outcomes, the observed proportion is influenced by the number of participants and by how common the event is. The normal approximation used in the planning illustration is a simplified method for estimating sample sizes. In general, when counts are sparse or event probabilities are near the boundaries of their possible range, approximation quality can be weaker; exact or model-based approaches may behave differently. No claim is made that the trial’s original design used the same planning assumptions. The original design assumptions are not reported in the registry record.

What is the role of imputation?

The primary endpoint description states that missing data were imputed with the Multiple Imputation method. In general, multiple imputation represents uncertainty about missing values by using more than one completed dataset and combining the resulting analyses. Its validity depends on assumptions about the missingness process and the imputation model. The registry record does not report the model specification, variables used, number of imputations, or sensitivity analyses, so those aspects cannot be assessed from the posted information. The reported primary result should therefore be understood alongside this incomplete reporting of imputation details.

Finally, the primary comparison is one of several outcomes. In general, examining many outcomes increases the chance that some results appear unusual by chance if each is considered separately. A prespecified hierarchy or multiplicity adjustment can help control that issue, but such details are not reported in the registry record. The primary endpoint remains the main stated efficacy question; secondary findings are supportive and should be interpreted with appropriate caution.

11. Confidence Intervals and Precision

Precision is reflected partly in the width of a confidence interval: narrower intervals indicate less sampling uncertainty under the specified method, while wider intervals indicate more. For the primary recalculated risk difference, the 95% confidence interval is 0.514 to 0.767. The estimate is 0.641. The interval does not include zero, so the unadjusted estimate is inconsistent with no risk difference under the calculation’s assumptions. Its width still matters: a range of plausible contrasts remains, and the point estimate should not be treated as exact.

The registry’s logistic-regression result is reported as a risk difference of 64.74, with a 95% confidence interval from 51.97 to 77.51. This is a distinct, sponsor-reported analysis and is expressed on a different scale from the recalculated decimal risk difference. Its interval also excludes zero. The methods and estimates should be kept paired with their own intervals rather than combining one analysis’s point estimate with the other analysis’s uncertainty limits.

Precision is influenced by the amount of information in the data, outcome frequency, and the analysis method. Here, the arm sizes differ, and the placebo responder percentage is low. General statistical reasoning cautions that sparse event information can make estimates less stable, especially for relative measures. The recalculated relative risk and odds ratio have wide confidence intervals, which signals substantial uncertainty about their magnitudes even though the estimated contrast is large. The risk difference is a more direct absolute summary for this endpoint.

Confidence intervals address sampling variability under their assumptions. They do not capture uncertainty from unreported model choices, missing-data assumptions, endpoint selection, or limitations in generalizability. The primary outcome used multiple imputation, but details needed to evaluate that procedure are not reported in the registry record. Thus, the interval is important evidence about statistical precision, but not a complete measure of all uncertainty surrounding the result.

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 these binary and continuous outcomes, the figures are participants per arm, not total events. The stated illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The trial’s own original sample-size justification is not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities for hypothetical future studies, not probabilities that the trial result is true and not estimates of the probability that this completed trial detected an effect.

Rows planning for 100% of the observed effect use the full observed contrast as the target; rows planning for 75% or 50% use smaller target effects. Smaller effects generally require more participants to detect with the same power and significance level, which is why the planning figures rise as the assumed fraction declines. The illustrations use the observed trial effect as an input, so unusually large observed effects can yield modest sample-size estimates that may not transport to a future study.

This is not observed power. Observed power is not a useful substitute for examining the estimate and its confidence interval after the data are collected. The planning figures instead show how sample-size requirements change under explicit hypothetical assumptions. They do not establish what the sponsor planned, what assumptions informed the original trial, or whether a future study would reproduce the observed effect.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.053; treatment proportion p₁ = 0.693; average p̄ = 0.373.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6839 = 1.3404.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5123 = 0.4312.
4. n = (1.3404 + 0.4312)² / (0.6407)² = 7.6, rounded up to 8 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 <- 0.0526315789473684                          # control proportion
p1 <- 0.693333333333333                          # 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(5176639)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 13 (80% power), 17 (90% power)
 50% of observed effect: n per arm = 25 (80% power), 33 (90% power)
power.prop.test: 7.6 
Simulated power at n = 8 per arm: 0.868 (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 a sponsor analysis using logistic regression, with risk difference as the reported measure. It gives a risk difference of 64.74, a 95% confidence interval from 51.97 to 77.51, and p < 0.001. The simple recalculation from the posted arm summaries gives a risk difference of 0.641, a 95% confidence interval from 0.514 to 0.767, and p <0.001. The recalculation is unadjusted; it is not a replacement for the registry’s analysis.

The two presentations differ in method and scale. The registry record does not report enough model detail to identify all reasons for the numerical difference, so no specific explanation should be assumed. The record does not flag a discrepancy. The sponsor analysis is the trial’s reported analysis, while the recalculation is a transparent summary-statistic comparison that can help readers understand the arm-level contrast.

Both analyses indicate a positive contrast favoring a higher observed responder proportion in the veligrotug arm, and both reported intervals exclude zero. Their p-values should be interpreted in relation to the method used, not as interchangeable precision measures. The registry’s modeled result should be read as the primary sponsor-reported inferential analysis; the unadjusted recalculation is supplementary context. Neither analysis establishes clinical importance on its own, and both remain subject to the endpoint, population, missing-data, and reporting limitations described elsewhere.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and lists secondary outcomes, but it does not report a multiplicity-control strategy. When a trial tests several outcomes, unadjusted p-values do not account for the number of opportunities to observe a result that appears statistically notable. In general, prespecifying a hierarchy or applying an adjustment can help control the overall false-positive risk. Without a reported plan, the primary result and secondary comparisons should not be assigned the same confirmatory status automatically.

The primary endpoint description states that missing data were imputed using the Multiple Imputation method. The record does not report the imputation model, assumptions about missingness, number of imputed datasets, or sensitivity analyses. Those details matter because results can depend on how missing outcomes are represented and on whether the assumptions are plausible. The reported primary percentages should be read with the stated imputation approach in mind, while recognizing that its implementation cannot be evaluated fully from the registry record.

The primary analysis population is defined as the mITT population: randomized participants who received at least 1 dose of study drug. The registry also notes that reported Ns count participants analyzed regardless of which eye was evaluated. The record does not provide further detail about exclusions from the randomized population, endpoint-specific missingness, or the handling of intercurrent events. Those omissions limit assessment of how closely the analyzed sample corresponds to all randomized participants and how robust the result is to alternative analysis choices.

The statistical analysis plan, interim-analysis details, original sample-size justification, and additional model specifications are not reported in the registry record. Their absence does not establish that these procedures were not conducted; it means their use and details cannot be assessed from the record. These reporting limits are relevant when distinguishing a strong observed contrast from a fully auditable account of all prespecified analyses.

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: arrhythmia (1.3%), hyperthyroidism (1.3%), appendicitis (1.3%), cellulitis (1.3%), hepatic enzyme increased (1.3%).

The posted serious adverse event figures report 7 participants affected in the veligrotug group and 0 in the placebo group. The corresponding groups at risk are reported as 75 and 38. The registry lists arrhythmia, hyperthyroidism, appendicitis, cellulitis, hepatic enzyme increased, and peripheral sensory neuropathy among the top serious terms, each at 1.3%. The record reports 0 deaths in each group.

These are descriptive safety counts. They do not by themselves show whether an event was caused by study treatment, how severe or prolonged it was, or whether participants had relevant medical history. Serious events can differ in type and clinical context, and a count alone does not characterize that context. The registry also reports other adverse events affecting 63 participants in the veligrotug group and 19 in the placebo group; those figures describe events classified separately from serious adverse events and should not be conflated with the serious-event counts.

The denominators are the reported participants at risk for each arm. The registry record does not provide enough detail in these figures to assess event timing, recurrent events, exposure-adjusted rates, or attribution. Safety interpretation should therefore remain descriptive and be considered alongside the trial’s efficacy results and the limits of the reported safety information. These counts do not establish a treatment effect on safety or determine an individual participant’s risk.

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

The primary results show that a larger proportion of participants assigned to veligrotug met the trial’s study-eye proptosis responder definition at Week 15 than participants assigned to placebo. The observed arm percentages and the positive risk-difference estimates provide a clear statistical contrast for this endpoint. The recalculated confidence interval excludes zero, and the registry’s modeled analysis also reports an interval excluding zero. These findings describe the trial’s evidence for the measured response under the tested regimen and analysis population.

That conclusion is narrower than saying that every participant improved, that all aspects of TED changed, or that a long-term benefit was established. The responder definition is based on a threshold change in proptosis, measured with an exophthalmometer, and assessed over the stated period. It does not describe each participant’s exact change, all symptoms, daily functioning, quality of life, durability, or outcomes beyond those listed in the registry. The trial’s other outcome measures address some additional dimensions, but results for every listed secondary outcome are not reported in the registry record.

The result also does not establish an individual participant’s likely response. Trial-level group comparisons summarize outcomes across the analyzed population; individual outcomes can differ. Generalization beyond the enrolled population, treatment schedule, endpoint definition, and assessment period requires evidence not contained in this comparison.

Statistical evidence is not the same as a complete clinical judgment. Effect size, precision, outcome relevance, safety, missing-data assumptions, and the multiplicity of outcomes all matter. The serious adverse-event figures are descriptive and do not settle causation or the overall balance of benefits and harms. Accordingly, the posted results support an interpretation of a higher observed primary responder rate in the veligrotug arm, while leaving broader efficacy, longer-term outcomes, and complete safety characterization unresolved by the information reported in the registry.

18. Why This Trial Matters Statistically

This trial offers a useful example of how a binary clinical endpoint can make a treatment contrast understandable while also simplifying the underlying measurements. The primary outcome translates change in proptosis into a responder classification based on a stated threshold and a condition for the fellow eye. Reporting both arm-level percentages and a risk difference allows readers to see the observed response proportions and their absolute contrast, rather than relying only on a significance test.

The registry also permits comparison between a sponsor-reported regression analysis and a simple unadjusted recalculation from the posted summaries. Keeping those analyses distinct illustrates an important statistical practice: results should be interpreted in relation to their methods, and estimates that share a broad label may not be directly interchangeable. The reported confidence intervals help convey uncertainty, while the missing model and imputation details show why precision estimates cannot answer every question about robustness.

Related secondary proptosis outcomes provide a way to assess whether the primary pattern appears across differing measurements and endpoint forms. At the same time, the collection of primary and secondary outcomes raises the need to understand prespecification and multiplicity. The registry record does not report those details, making cautious interpretation especially important.

Finally, the planning illustrations connect observed effects to hypothetical sample-size requirements, but they are not evidence of the trial’s original design rationale or observed power. Together, these features make the trial statistically informative as a case study in binary endpoints, modeled versus unadjusted estimates, uncertainty, missing-data reporting, and the interpretation of multiple outcomes. The value lies in examining what the posted analysis can support and where the record leaves questions open.

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.

Several limitations are specific to interpreting this trial from the registry record. The primary endpoint is a threshold-based response, so it can obscure the distribution of individual changes and may classify participants near the threshold differently from those with larger changes. The primary outcome is tied to the study eye and an exophthalmometer measurement; other outcome definitions use different eyes or imaging methods, which makes direct equivalence across measures inappropriate.

The primary analysis includes randomized participants who received at least 1 dose, rather than being described simply as all randomized participants. The registry says the reported Ns count participants analyzed regardless of which eye was evaluated, but it does not give further detail about missingness by arm or endpoint. Although missing primary data were imputed using Multiple Imputation, the model, assumptions, and sensitivity analyses are not reported in the registry record.

The registry’s sponsor analysis is identified as logistic regression with risk difference reported, but detailed model specifications are not reported. The simple recalculations are unadjusted and cannot recover information about covariate adjustment or other features of the sponsor model. Further, the registry does not report a multiplicity strategy, making the secondary results less suitable for stand-alone confirmatory claims. Numerical results are not reported for every listed secondary outcome.

Safety reporting in the listed figures is also limited: event counts do not establish causality, timing, recurrence, or exposure-adjusted rates. The record does not report the original sample-size justification, interim analyses, or full statistical analysis plan. These limitations concern what can be evaluated from the registry record; they do not prove that unreported procedures or analyses were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Safety, Tolerability, and Efficacy Study of Veligrotug (VRDN 001) in Participants With Thyroid Eye Disease (TED) — NCT05176639.
• Registry record last updated 2026-08-13; status last verified 2026-07.
• Results first posted 2026-08-13.
• 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

NCT05176639 is a completed randomized, triple-masked, parallel-group phase 3 trial of veligrotug versus matched placebo in participants with thyroid eye disease. The registry lists enrollment of 113 and describes the primary outcome as the study-eye proptosis responder rate from baseline to Week 15, measured by exophthalmometer.

The posted primary percentages were 70.0% for veligrotug and 5.26% for placebo. The sponsor-reported logistic-regression risk difference was 64.74, with a 95% confidence interval from 51.97 to 77.51 and p < 0.001. The unadjusted recalculation reports a risk difference of 0.641, with a 95% confidence interval from 0.514 to 0.767 and p <0.001.

The registry lists additional proptosis, clinical activity, overall response, and diplopia outcomes, alongside safety, tolerability, pharmacokinetic, and pharmacodynamic objectives. Multiplicity planning, detailed model and imputation specifications, and the trial’s original sample-size justification are not reported in the registry record. Serious adverse events were reported for 7 participants in the veligrotug group and 0 in the placebo group; no deaths were reported.