A Study to Investigate the Long-term Safety, Tolerability, and Efficacy of Rozanolixizumab in Adult Patients With Generalized Myasthenia Gravis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Investigate the Long-term Safety, Tolerability, and Efficacy of Rozanolixizumab in Adult Patients With Generalized Myasthenia Gravis (NCT04124965), a randomized phase 3 study. The primary outcome is Percentage of Participants With Treatment-emergent Adverse Events (TEAEs).

2. Clinical Question

The central statistical question is descriptive: how often were treatment-emergent adverse events recorded in each dosage grouping, and how uncertain is the difference between those percentages? Because both groups received rozanolixizumab, this is not a comparison of treatment with no treatment. It also does not isolate a long-term treatment effect from changes over time, the natural course of the condition, or other influences. Random assignment can support a comparison between assigned regimens, but open-label treatment and permitted dose switching make careful attention to the actual analysis grouping important. The registry states that the primary endpoint was planned for analysis by most recent dose received at or before adverse-event onset. The complete details of how switching participants were classified are not reported in the registry record.

3. Trial Design

This completed Phase 3 study was a randomized, open-label extension study of rozanolixizumab in adults with generalized myasthenia gravis. Its stated purpose was to investigate long-term safety, tolerability, and efficacy. The registry reports enrollment of 71 participants. The study began on 2019-10-29, and primary completion was recorded as 2021-09-01.

Participants were assigned to one of two rozanolixizumab dosage regimens, approximately 7 mg/kg or approximately 10 mg/kg. The arm descriptions say that participants received their assigned dosage at pre-specified time points during the treatment period, with the possibility of switching regimens at investigator discretion. There was no masking. The registry identifies randomization as the allocation method, but the randomization procedure and details such as stratification are not reported in the registry record.

The record labels the study model single group even though it also lists two randomized dosage regimens. It does not explain the model label, so the most defensible description is that the posted endpoint results compare two dosage groupings within a rozanolixizumab extension study. Neither is a placebo or untreated control. The primary safety endpoint uses a safety population described as randomized participants who received at least one dose. Its planned analysis grouped participants according to the most recent dose received at or before an adverse event began. The registry’s description of how participants who switched doses were handled is incomplete, and the full analysis-population rules are not reported.

The endpoint timeframe runs from baseline through the end of the study, up to Week 60; the adverse-event definition can extend up to 8 weeks after the last dose for participants who discontinued. The registry lists additional outcomes concerning changes in MG-ADL, MG-C, and QMG total scores, as well as use of rescue medication. The complete statistical analysis plan, including the original sample-size justification and any planned interim analyses, is 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: Participant Flow refers to the Randomized Set.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Safety Set (SS) consisted of all randomized study participants who received at least 1 dose of IMP in this study. This endpoint was planned to be analyzed using the SS by most recent dose received i.e. the most recent dose received at or before the AE onset. Participants who switched doses were counted in both rozanolixizumab (RLZ) doses.

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: Baseline Characteristics refer to the Randomized Set (RS) which consisted of all study participants who were randomized, using the treatment assigned instead of the actual treatment received.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Treatment-emergent Adverse Events (TEAEs), measured over From Baseline until End of Study (up to Week 60).

The primary endpoint is the percentage of participants with treatment-emergent adverse events (TEAEs). It is a safety measure: it counts participants with an event meeting the registry definition during the stated observation period, rather than measuring a change in a symptom score or a time until an event occurs.

The definition includes an adverse event beginning on or after the first administration of investigational medicinal product. It also includes an unresolved event already present before the first administration if that event worsened in intensity after exposure. For participants who discontinued the study or investigational product, the definition extends up to 8 weeks after the last dose. The endpoint timeframe is from baseline until the end of study, up to Week 60.

A percentage is useful for describing how common an event was among participants in a defined safety population. It gives a direct summary of participant-level occurrence, but it does not convey how many events each participant experienced, how severe every event was, or when events occurred. Those details require other safety summaries. The endpoint is also not, by itself, proof that an event was caused by the study drug: the registry definition identifies events by timing and worsening criteria, not by establishing causation.

The registry says this outcome was planned for analysis in the safety set and by the most recent dose received at or before event onset. Because dose switching was permitted, interpretation depends on that grouping rule. The record’s description of the handling of participants who switched doses is incomplete, so the posted dose-specific percentages should be read as the recorded analysis groupings rather than assumed to represent an entirely separate set of participants in each regimen.

7. Results Posted in the Registry

• Rozanolixizumab ~10 mg/kg: 78.6% (33/42) versus 76.0% (38/50) on control; risk difference 2.6 percentage points (95% CI -14.6 to 19.7), risk ratio 1.03 (0.83–1.29); unadjusted two-proportion z-test p = 0.770.

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 Using Rescue Medication (Intravenous Infusion of Immunoglobulin G (IVIg) or Plasma Exchange (PEX))

• 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:
  • Rozanolixizumab ~10 mg/kg: 0.0% (0/35) versus 11.4% (4/35) on control; risk difference -11.4 percentage points (95% CI -22.0 to -0.9); unadjusted two-proportion z-test p = 0.039.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rozanolixizumab ~10 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes spanning symptom and function scores—MG-ADL, MG-C, and QMG—and the use of rescue medication. These outcomes address different aspects of the study’s stated interest in longer-term efficacy and clinical course, while the primary endpoint is a safety summary. They therefore complement the TEAE result but do not answer the same question. An efficacy-oriented score change cannot by itself confirm or overturn a safety comparison, and the primary safety percentages do not describe symptom change.

The registry describes the score outcomes as changes from baseline at scheduled assessments during treatment and observation periods. Their full posted numerical results and analyses are not available in the record summary used for this interpretation; the displayed endpoint listings include the rescue-medication comparison. The overall secondary-outcome pattern should consequently be read as a set of distinct measures rather than compressed into a single conclusion about efficacy. The registry record does not report a combined analysis across those outcomes.

The rescue-medication comparison has an unadjusted p-value of 0.039. This is a secondary result, and it sits within a family of multiple secondary measures and assessments. When many outcomes or time points are examined, the chance of at least one apparently unusual result can increase. The record does not report a multiplicity adjustment or a prespecified hierarchy that would establish this comparison as confirmatory. Its unadjusted result therefore carries less weight than a single prespecified primary test with a clearly reported analysis plan.

That caution does not mean the secondary result should be discarded. It means it should be considered as one piece of evidence, with attention to the low event counts, the study design, and the other outcomes. The registry does not report adjusted secondary analyses, full missing-data methods, or a detailed account of how all scheduled assessments entered the analyses. As a result, the secondary endpoints can add context, but they cannot by themselves settle the interpretation of the primary safety comparison or support a broad claim about long-term efficacy.

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

• Change From Baseline in Myasthenia Gravis-Activities of Daily Living (MG-ADL) Total Score at Each Scheduled Assessment During Treatment and Observation Periods
• Change From Baseline in Myasthenia Gravis-Composite (MG-C) Total Score at Each Scheduled Assessment During Treatment and Observation Periods
• Change From Baseline in Quantitative Myasthenia Gravis (QMG) Total Score at Each Scheduled Assessment During Treatment and Observation Periods
• Percentage of Participants Using Rescue Medication (Intravenous Infusion of Immunoglobulin G (IVIg) or Plasma Exchange (PEX))

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the TEAE definition during the stated observation period or did not. The displayed percentage summarizes the number of participants with an event relative to the denominator used for that dosage grouping. The registry describes the intended safety population as randomized participants who received at least one dose, and says that grouping for this endpoint was based on the most recent dose received at or before the adverse event began.

What does a risk difference express?

General statistical explanation: a risk difference subtracts one event proportion from another. It is expressed on the proportion scale, so a value of zero corresponds to equal proportions in the two groups. A positive or negative value indicates the direction of the estimated difference according to the comparison’s specified ordering. For this comparison, the estimate is 0.026 for the approximately 10 mg/kg group relative to the approximately 7 mg/kg group. The direction and magnitude are estimates from the posted participant counts, not proof of a causal effect.

How should the p-value be read?

General statistical explanation: a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The primary comparison’s unadjusted p-value is 0.77. That result does not provide strong evidence against equality under the test, but it does not prove equality or rule out meaningful differences. The registry record does not report the full testing procedure or whether the displayed analysis was prespecified in all its details.

What does the confidence interval add?

General statistical explanation: a confidence interval describes uncertainty around an estimate and identifies a range of values compatible with the data under the interval method. The posted interval for the primary risk difference crosses zero, so the data are compatible with values in either direction as well as no difference. The confidence level and interval-construction method are not reported in the registry record. The interval should not be treated as a probability statement about the true value without specifying a statistical framework.

Why does dose switching matter?

The arm descriptions explicitly allow a regimen switch at investigator discretion. The primary endpoint plan refers to the most recent dose received at or before the event began. This is a dose-at-event grouping, not necessarily a comparison based solely on the initially assigned regimen. In general, switching can affect interpretation because participants may contribute to a different dose grouping than their initial assignment, and the reasons for switching may be related to their clinical course or tolerability. The record does not report enough detail to determine how switching was handled in every case or to reconstruct a full intention-to-treat analysis.

What can be said about analysis choices?

The posted comparison is unadjusted. The registry lists no reported analyses for the secondary outcome entries. The statistical model, confidence-interval method, missing-data procedures, and any covariate adjustment are not reported in the registry record. No assumption about a particular regression method or imputation approach should be made from the reported percentages alone. The study’s original sample-size justification and any interim-analysis plan are also not reported.

General statistical explanation: for binary outcomes, the amount of information depends not only on the percentage but also on the number of participants and the number of observed events. When event proportions are close, uncertainty can remain substantial, especially when group denominators are limited. A confidence interval helps show that uncertainty; a point estimate alone does not. The primary comparison’s interval includes zero and spans values on both sides, illustrating why the estimated difference should not be treated as precise evidence of a directional contrast.

General statistical explanation: over-dispersion matters most in settings where variability exceeds what a chosen model assumes, often because observations are more heterogeneous or dependent than expected. A simple participant-level binary summary does not itself establish that over-dispersion is present. The registry does not report a model-based analysis of over-dispersion for this endpoint, so there is no basis to claim that it was detected, corrected, or relevant to the posted comparison.

The record includes a planning illustration based on the observed effect for a hypothetical two-arm study. It is not a report of the original design rationale. The assumptions accompanying that illustration are distinct from the unreported trial-specific planning choices. Likewise, the displayed comparison and its p-value are not a substitute for a full statistical analysis plan: prespecification, multiplicity control, missing-data handling, and analysis-population details remain important for judging how confirmatory the findings are.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.026, but the confidence interval extends across zero, from the negative side to the positive side. That interval is important because it shows that the point estimate alone gives an incomplete account of the comparison. The data are compatible with a range of possible differences, including a value of no difference and values in either direction. The unadjusted p-value of 0.77 is consistent with the lack of a clear statistical distinction between the dosage groupings.

The posted percentages, 76.0% and 78.6%, are descriptive estimates for the listed denominators of 50 and 42. Their displayed precision should not be confused with certainty about the underlying event rates. An estimate can be stated to a decimal place while remaining uncertain. The registry does not report the confidence interval for each group’s individual percentage, and the interval confidence level and construction method for the comparison are not reported in the registry record.

Precision is also affected by how participants are grouped. The endpoint plan refers to the most recent dose received at or before an event began, and the regimen could be switched. The registry’s account of participants who switched is incomplete. This means the denominators should be interpreted according to the posted analysis rather than as proof that every participant remained in one distinct dose group throughout follow-up.

Overall, the comparison is not precise enough to support a firm directional conclusion. The interval does not establish equivalence, because no equivalence margin is reported and the interval includes a range of possible differences. Nor does its crossing zero show that the groups are identical. It indicates uncertainty around the estimated contrast, which should be considered together with the open-label extension design and the limits of the registry’s analysis details.

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 display is a planning illustration based on the observed effect, not the trial’s original design calculation. For this binary outcome, the entries are participants per arm, not total events. The accompanying assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to be detected is set to the stated fraction of the observed effect. The original study’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under its assumptions, if that effect were the true one. The 90% power column gives the analogous planning count for a 90% chance. These are conditional design calculations, not predictions that a future study will produce a particular result. They depend on the assumptions used, including the selected effect size and the statistical test framework.

Rows planning for a smaller fraction of the observed effect require more participants per arm than rows planning for the full observed effect. This is a general feature of power calculations: smaller differences are harder to distinguish from random variation, so more information is needed. The displayed planning counts become very large because the observed difference between the groups is small. The curve is another way of illustrating how planned sample size changes with the effect targeted; it does not change the assumptions or make the calculation a result from the completed study.

These figures are not observed power. Observed power is not a useful substitute for examining the estimate and its confidence interval after a study; the planning illustration is meant to show what a hypothetical design might require under stated assumptions. It should not be read as evidence about the actual power of this extension study or as a reconstruction of its original protocol.

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 = 0.760; treatment proportion p₁ = 0.786; average p̄ = 0.773.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5925 = 1.1613.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5923 = 0.4985.
4. n = (1.1613 + 0.4985)² / (0.0257)² = 4,166.4, rounded up to 4,167 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 <- 0.76                          # control proportion
p1 <- 0.785714285714286                          # 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(4124965)
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 = 4,167 (80% power), 5,578 (90% power)
 75% of observed effect: n per arm = 7,482 (80% power), 10,016 (90% power)
 50% of observed effect: n per arm = 16,999 (80% power), 22,756 (90% power)
power.prop.test: 4166.4 
Simulated power at n = 4,167 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes, including three score-based measures and rescue-medication use. The score outcomes are assessed at scheduled times during treatment and observation, which also creates repeated assessments. The record does not report whether the study controlled the overall type I error across outcomes and time points, used a hierarchical testing strategy, or designated particular secondary analyses as confirmatory. The unadjusted secondary p-value should therefore be treated as exploratory evidence rather than interpreted as if it were the sole planned test.

Missing-data procedures are not reported in the registry record. This matters because participants may not have observations at every scheduled assessment, and the registry lists follow-up across treatment and observation periods. Without the analysis methods, it is not possible to determine how incomplete score assessments or missing endpoint data were handled, whether any imputation was used, or what assumptions underlie the posted secondary summaries. No missingness rate should be inferred from the endpoint denominators alone.

The primary safety population is described as randomized participants who received at least one dose. The endpoint analysis was planned according to the most recent dose received at or before the onset of an adverse event. Participants could switch regimens at investigator discretion, and the registry’s explanation of how those participants were handled is truncated. The full analysis-population rules, including the relationship between randomization, treatment received, and each listed denominator, are not reported in the registry record.

The registry reports enrollment of 71, while the primary endpoint group listings show denominators of 50 and 42. Because the planned endpoint grouping uses most recent dose and dose switching was allowed, those denominators should not automatically be treated as mutually exclusive participant counts. The record does not fully reconcile enrollment with the endpoint-specific groupings, so the exact participant flow cannot be reconstructed from these entries alone.

The protocol’s original sample-size justification, interim-analysis plan, statistical model, adjustment strategy, and detailed rules for handling deviations are not reported in the registry record. These omissions do not invalidate the descriptive figures, but they limit assessment of how closely the posted analyses follow the planned inferential framework. A cautious reading distinguishes registry-reported summaries from a complete account of the trial’s statistical plan.

15. 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: myasthenia gravis (6.0%), pericarditis (2.4%), cardiac failure congestive (2.0%), retinal detachment (2.0%), biopsy kidney abnormal (2.0%).

The registry lists serious adverse event counts of 7 among 50 participants in the approximately 7 mg/kg group and 2 among 42 participants in the approximately 10 mg/kg group. It lists zero deaths in each group. These are participant counts in the posted safety summaries; they are not adjusted comparisons and do not, by themselves, establish a difference in risk between regimens.

The registry also names serious-event terms, including myasthenia gravis and pericarditis, alongside several other terms. The listed term percentages should be read as reported safety summaries, not as estimates of causal risk. The record does not provide enough detail in these entries to determine whether a participant could contribute to more than one term or to reconstruct event timing and clinical context.

Serious adverse events are distinct from the primary TEAE endpoint, which counts participants with any event meeting its broader timing and worsening definition. Serious-event counts do not describe all TEAEs, and the TEAE percentages do not specify how many events were serious. The absence of listed deaths does not establish the absence of other important harms. Safety interpretation should remain descriptive because both groups received rozanolixizumab, the study was open-label, and the registry does not provide a controlled comparison with an untreated group.

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

The posted primary outcome shows that TEAEs were recorded in 76.0% of the approximately 7 mg/kg group and 78.6% of the approximately 10 mg/kg group. The estimated risk difference is small in the direction of a higher percentage in the approximately 10 mg/kg grouping, but its confidence interval includes zero and the unadjusted p-value is 0.77. The evidence does not clearly distinguish the two groupings on this endpoint.

That interpretation is narrower than saying the regimens are the same. A non-significant comparison does not demonstrate equivalence, and the registry reports no equivalence margin. The uncertainty interval permits values on either side of zero, so a range of underlying differences remains compatible with the data. The result also does not show that either regimen is safe in an absolute sense; a percentage with at least one TEAE is only one summary of safety, and it does not explain the nature, severity, timing, or consequences of every event.

Nor does this study establish what would have happened without rozanolixizumab. Both study groups received the drug, and the study was open-label. The randomized comparison is between dosage regimens within an extension study, not between active treatment and placebo or no treatment. Dose switching was permitted, and the endpoint grouping was based on the most recent dose received at or before event onset. The registry does not fully describe the consequences of that rule for participants who switched.

The secondary outcomes offer additional perspectives, but the registry does not report multiplicity adjustment or enough analysis detail to treat the unadjusted secondary result as definitive. The findings are best understood as descriptive registry evidence with uncertainty, population and grouping limitations, and an incomplete account of the statistical plan. They do not amount to medical advice or a basis for individual treatment decisions.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between a point estimate and the uncertainty around it. The TEAE percentages are close, but the main interpretive issue is not simply whether one percentage is numerically higher. The risk-difference interval crosses zero, and the unadjusted p-value is 0.77, so the comparison does not clearly identify a difference between the two dosage groupings. At the same time, the result does not establish equivalence.

The design also highlights the importance of understanding the analysis population and exposure classification. The study was randomized, yet the registry describes the primary endpoint grouping by most recent dose at or before an event, and participants could switch regimens. That is not necessarily the same as comparing participants strictly by their initial randomized assignment. When the endpoint grouping is not fully described, a reader cannot assume that the listed denominators are independent, fixed groups throughout follow-up.

The registry’s secondary result illustrates why multiplicity matters. An unadjusted p-value can look notable when many outcomes or assessment times are considered, but its evidential weight depends on what was prespecified and how the family of tests was handled. Those details are not reported. Finally, the planning illustration shows how a small target difference can require substantially more participants than a larger one under the stated hypothetical assumptions. It must not be mistaken for the original design rationale or the study’s observed power.

Together, these points show why registry results require attention to endpoint definitions, denominators, uncertainty, switching, and the distinction between descriptive and confirmatory analyses. They help frame what the posted summaries can support without overstating what they establish.

18. 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.

This is an open-label extension study with two rozanolixizumab dosage regimens and no placebo or untreated comparison group. As a result, the primary safety comparison is not a direct estimate of treatment versus no treatment, and the study design cannot by itself separate treatment-associated events from events that might occur for other reasons. The endpoint definition is based on timing and worsening after exposure, but that definition does not establish causation.

Dose switching was allowed at investigator discretion. The primary endpoint plan groups by the most recent dose received at or before event onset, while the record’s explanation of switch handling is incomplete. This leaves uncertainty about the relationship between randomized assignment, received regimen, and the posted denominators. The enrollment count and endpoint group denominators are not fully reconciled in the record.

The registry record does not report the confidence-interval method or confidence level, missing-data procedures, detailed statistical model, multiplicity strategy, or the complete analysis-population rules. It also does not report the original sample-size justification or any interim-analysis plan. Those gaps limit evaluation of prespecification and the robustness of inferential results. The posted secondary comparison is unadjusted, and several secondary outcomes and scheduled assessments are listed.

Finally, the primary endpoint is a participant-level percentage and does not convey event counts per participant, timing, duration, or severity for all TEAEs. The serious-event summary is a separate safety description and cannot fill in those details. These limitations call for a restrained reading of the findings as registry-posted summaries rather than a comprehensive account of long-term safety or efficacy.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Investigate the Long-term Safety, Tolerability, and Efficacy of Rozanolixizumab in Adult Patients With Generalized Myasthenia Gravis — NCT04124965.
• Registry record last updated 2026-08-20; status last verified 2026-08.
• Results first posted 2023-08-21.
• 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.

22. Record Summary

The registry record describes a completed, randomized, open-label Phase 3 extension study of rozanolixizumab in adults with generalized myasthenia gravis. Enrollment was 71. Participants were assigned to approximately 7 mg/kg or approximately 10 mg/kg regimens, with dose switching allowed at investigator discretion.

The primary endpoint was the percentage of participants with TEAEs from baseline until the end of study, up to Week 60. The posted percentages were 76.0% and 78.6%, with a risk-difference comparison whose confidence interval includes zero and an unadjusted p-value of 0.77. The registry also lists serious adverse events and secondary outcomes covering symptom scores and rescue-medication use.

Interpretation is limited by the open-label extension design, the absence of a placebo or untreated group, incomplete information about switching and analysis populations, and unreported statistical-plan details. The posted results describe the registry’s endpoint summaries; they do not establish equivalence or a treatment effect relative to no treatment.