A Study to Evaluate Safety and Efficacy of Ocrelizumab in Comparison With Fingolimod in Children and Adolescents With Relapsing-remitting Multiple Sclerosis (RRMS): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Safety and Efficacy of Ocrelizumab in Comparison With Fingolimod in Children and Adolescents With Relapsing-remitting Multiple Sclerosis (RRMS) (NCT05123703), a randomized phase 3 study. The primary outcome is Protocol-defined Annualized Relapse Rate (ARR).

2. Clinical Question

The central statistical question concerns the rate of relapses over participants' observed time at risk, rather than simply the proportion of participants who experience at least one relapse. The registry reports treatment-specific rate estimates and confidence intervals, as well as an adjusted rate ratio for the sponsor's analysis. Those quantities address related but distinct questions: the arm-level estimates describe the rate in each group, while a rate ratio compares the groups. The trial also includes safety, imaging, pharmacokinetic, immunogenicity, and blood-cell outcomes, but those measures do not replace the primary relapse-rate question.

3. Trial Design

This is a randomized, parallel-group Phase III study sponsored by Hoffmann-La Roche. The registry lists quadruple masking and describes the study as double-blind and double-dummy. In a double-dummy design, each treatment group receives its assigned active treatment together with a matching placebo for the other treatment, helping preserve masking despite different treatment routes or schedules. Here, ocrelizumab is administered by intravenous infusion and fingolimod orally.

The registry lists enrollment of 188. The study began on 2022-05-19, has primary completion recorded as 2025-06-09, and has status active, not recruiting. These are registry dates and status, not a report that all study follow-up or every analysis is complete. The planned double-blind period is described as continuing until after the last randomized participant has completed 24 weeks. The primary outcome timeframe extends until after that participant completed 24 weeks since first study treatment administration, up to approximately 160 weeks.

The primary population is the full analysis set, defined in the registry as all randomized participants, analyzed according to assigned treatment. This is an intention-to-treat-style grouping for the stated population definition, though additional details about exclusions or analysis-specific populations are not reported in the registry record. The record does not report the original sample-size justification, target effect used in designing the trial, or the assumptions used for its design.

The intervention descriptions specify the treatment schedule, but the registry record does not give complete dose amounts in the listed descriptions. The primary measure is protocol-defined annualized relapse rate. Other listed outcomes include relapse rate, MRI lesion measures, adverse events, ocrelizumab exposure measures, anti-drug antibodies, and CD19-positive B-cell counts. The registry's listed secondary measures and analyses should be distinguished from the primary noninferiority assessment; the presence of an outcome in the registry does not by itself establish that numerical results are posted for it.

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 ocrelizumab + fingolimod placebo or fingolimod + ocrelizumab placebo. The study is still ongoing.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all randomized participants, with participants grouped according to their assigned treatment.

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: Full Analysis Set (FAS) included all randomized participants, with participants grouped according to their assigned treatment.

6. Primary Endpoint

The registry lists the primary outcome as Protocol-defined Annualized Relapse Rate (ARR), measured over Up to after the last participant randomized completed 24 weeks since first study treatment administration (up to approximately 160 weeks).

The primary endpoint is protocol-defined annualized relapse rate (ARR), expressed as relapses per patient-year. ARR is calculated as the total number of qualifying relapses divided by total patient-years. This rate incorporates both the number of events and the amount of observation time, which is useful when participants contribute different lengths of follow-up.

A relapse is defined in the registry as new or worsening neurological symptoms attributable to multiple sclerosis, after a relatively stable or improving neurological state for at least 30 days. Symptoms must persist for >24 hours and not be attributable to confounding clinical factors. The symptoms must also be accompanied by objective neurological worsening: an increase of at least half a step on the expanded disability status scale, or the specified change in one or more functional-system scores. The affected functional system may be pyramidal, ambulation, cerebellar, brainstem, sensory, or visual.

Using a protocol definition is important because the outcome depends on what qualifies as an event. A consistent definition helps distinguish relapses from temporary symptoms or changes that do not meet the specified criteria. General statistical context: an event rate is a count relative to accumulated exposure time; it is not the same quantity as the percentage of participants with an event.

The registry describes the population-level summary as a rate ratio and states that adjusted values were reported. The primary outcome timeframe runs until after the last randomized participant completed 24 weeks since first treatment, up to approximately 160 weeks. The record does not report more detail about the adjustment model or how incomplete observation time was handled.

7. Results Posted in the Registry

• Fingolimod: 0.14 versus 0.07 (relapses per patient-year) on control; rate ratio 1.93 (95% CI 0.76–4.89, derived from the posted confidence limits); p ≈ 0.167.

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.

Protocol-defined ARR

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Fingolimod: 0.14 versus 0.07 (relapses per patient-year) on control; rate ratio 1.93 (95% CI 0.76–4.89, derived from the posted confidence limits); p ≈ 0.167.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Fingolimod and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning relapse rate, MRI lesion counts, adverse events, ocrelizumab concentration and exposure, anti-drug antibodies, and CD19-positive B-cell counts. These outcomes address different aspects of disease activity, safety, treatment exposure, and biological response. A broad set of measures can add context to a primary endpoint, but each outcome answers its own question and may use a different analysis method.

Numerical results for the listed secondary outcomes other than the posted ARR analysis are not reported in the registry record. The ARR entry appears again among the secondary results and includes an adjusted rate ratio, confidence interval, and Wald Test p-value. It should not be mistaken for a set of results across all the distinct secondary measures. Without their estimates and uncertainty, no overall direction or consistency across the secondary endpoints can be assessed.

The secondary measures could help contextualize the primary relapse-rate result if their results and analysis details were available. For example, imaging outcomes assess lesion counts, while pharmacokinetic and immunogenicity measures address exposure and immune response. Their meaning is not interchangeable with ARR, and an unreported result cannot be taken as evidence for or against the primary finding.

Secondary analyses also commonly involve multiple outcomes and comparisons. General statistical explanation: when many hypotheses are examined, the chance of finding at least one apparently notable result by chance can increase unless multiplicity is addressed. The registry record does not report a multiplicity adjustment or a hierarchy governing secondary testing. Consequently, any unadjusted secondary result would generally carry less confirmatory weight than a prespecified primary result, and the registry does not provide enough information to determine how secondary inferences were controlled. No conclusion about a pattern across secondary endpoints is warranted from the posted numerical results.

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

• Protocol-defined ARR
• Number of New or Enlarging T2-hyperintense Lesions (T2 Lesions), as Detected by Brain Magnetic Resonance Imaging (MRI)
• Number of T1 Gd Lesions at Week 12
• Number of Participants With Adverse Events (AEs)
• Maximum Serum Concentration (Cmax) of Ocrelizumab
• Area Under the Plasma Concentration-time Curve Over a Dosing Interval (AUC Tau) of Ocrelizumab
• Number of Participants With Anti-drug Antibodies (ADAs) to Ocrelizumab
• Levels of Cluster of Differentiation 19 (CD19) + B-cell Count in Blood

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a rate, so the analysis concerns events relative to time under observation. The registry defines ARR as total protocol-defined relapses divided by total patient-years. A rate ratio compares the rate in one treatment group with the rate in the other. A rate ratio of 1 represents equal rates; values on either side indicate different relative rates, subject to the comparison's direction. The sponsor reports an adjusted rate ratio, while the simple re-calculation uses the arm-level rates without adjustment.

What does adjustment mean?

General statistical explanation: an adjusted estimate accounts for specified variables or features of the analysis, rather than comparing groups only through their raw summary rates. Adjustment can alter both an estimate and its uncertainty. The registry says adjusted values were reported, but the adjustment variables, model specification, and estimation details are not reported in the registry record. The adjusted result therefore can be described as posted, but the precise role of each model component cannot be evaluated from the registry description.

The posted sponsor estimate is an adjusted rate ratio of 0.517 with a 95% confidence interval of 0.193 to 1.329. The re-calculated estimate is an unadjusted Fingolimod-to-ocrelizumab rate ratio of 1.929. They use different adjustment status and opposite comparison orientations. Even when two estimates concern the same endpoint, they should be compared only after accounting for how each was defined and analyzed. The registry does not report enough model detail to reproduce the sponsor's adjustment.

Why use a confidence interval?

General statistical explanation: a confidence interval communicates the range of effect values reasonably compatible with the data and the analysis method at the stated confidence level. It conveys precision as well as direction. A narrow interval is more precise than a broad one, while a broad interval leaves more possible values compatible with the observed data. A confidence interval is not a probability statement that the true value lies in the particular reported interval.

For a rate ratio, 1 is the value corresponding to equal rates. A confidence interval that includes 1 does not exclude equal rates at the corresponding confidence level, although it also does not prove equality. It can include values representing different rates in either direction. The reported adjusted interval includes 1; the unadjusted re-calculation's interval also includes 1. The registry's primary description labels the sponsor analysis noninferiority, but that framework requires a prespecified margin and decision rule. Neither is reported in the registry record, so the interval cannot be assessed against the noninferiority criterion.

What is the unadjusted re-calculation?

The re-calculation uses the posted summary rates and is explicitly unadjusted. It is not a replacement for the sponsor's analysis or a reconstruction of the trial's full model. The reported unadjusted p-value is 0.167. A p-value describes how compatible the observed data are with a specified null model under the test assumptions; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. The exact testing details for the sponsor's primary noninferiority analysis are not reported in the registry record.

Rate outcomes can be more variable than a simple model assumes. General statistical explanation: over-dispersion occurs when event counts vary more than expected under a model's assumptions. If present and not accommodated, it can affect uncertainty estimates and tests. The registry lists a Poisson-based approach for the simple re-calculation, but the record does not report a diagnostic for over-dispersion or enough detail to establish whether the sponsor's model addressed it. No conclusion about over-dispersion in these trial data can be drawn from the posted information.

How does noninferiority differ from superiority?

General statistical explanation: a superiority analysis asks whether the data support a difference in a specified direction or any difference, according to its test. A noninferiority analysis asks whether the treatment being evaluated is not worse than the comparator by more than a prespecified margin. That margin must be stated and used in the interpretation. The registry labels the primary adjusted ARR analysis noninferiority and also lists an ARR analysis labeled superiority. The noninferiority margin and the fuller analysis plan are not reported in the registry record. The secondary ARR analysis reports a Wald Test, an adjusted rate ratio, a confidence interval, and a p-value, but those entries do not supply the missing primary noninferiority decision rule.

The registry identifies the full analysis set as all randomized participants grouped by assigned treatment. This definition helps clarify which participants the primary outcome population includes. The record does not report details about missing-data handling, censoring of exposure time, imputation, sensitivity analyses, or whether additional analysis populations were used for other outcomes. Those omissions matter because incomplete outcome observation and analysis choices can affect both rate estimates and their precision.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. The arm-level 95% confidence interval for ocrelizumab is 0.034 to 0.144 relapses per patient-year; for fingolimod it is 0.075 to 0.243. Both intervals cover a range of plausible arm-level rates, rather than a single known value. The rate estimates should therefore not be read as exact descriptions of the underlying rates.

The direct adjusted comparison has a 95% confidence interval of 0.193 to 1.329. It spans values below and above 1, the equal-rate value. This means the posted interval is compatible with a range of relative-rate interpretations, including no difference. The interval does not, by itself, establish equivalence, noninferiority, or superiority. In particular, noninferiority depends on a margin that is not reported in the registry record.

The unadjusted re-calculation also has an interval that includes 1. Its lower endpoint is reported as 0.760, so it is not repeated because the displayed precision limit is three decimal places. The broad interval indicates that the summary-rate comparison is not estimated with high precision. The exact precision of an estimate depends on the event information and exposure time, not enrollment alone.

General statistical context: confidence intervals describe uncertainty under the assumptions of the analysis. They do not capture every possible source of uncertainty, such as unreported model choices, measurement issues, or missing-data mechanisms. Because the registry does not provide all model and missing-data details, interpretation of the intervals is limited to the reported analyses and definitions. The arm-level intervals should also not be used as a substitute for the interval on the treatment contrast.

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 participants per arm, not total events. They are illustrations calculated from the observed effect, not the trial's original design calculations. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the assumed effect under those planning assumptions, if that effect and the model assumptions were correct. The 90% power column expresses the corresponding planning target with a higher chance of detection. These are prospective planning concepts, not evidence about what happened in the completed or ongoing trial.

For planning at 100% of the observed effect, the illustration gives 859 participants per arm for 80% power and 1,149 for 90% power. At 75% of the observed effect, it gives 1,619 and 2,167 participants per arm, respectively. At 50% of the observed effect, it gives 3,889 and 5,206 participants per arm, respectively. The pattern illustrates that smaller effects require more participants to detect under the same assumptions.

These figures are not observed power. They do not tell whether the trial achieved a particular probability of detecting its result, and they should not be used to reinterpret the study's observed estimates. They are planning illustrations based on the observed effect and specified assumptions, rather than a record of the trial's prospective design rationale. Because the original design assumptions are not reported, the planning illustration cannot establish why enrollment was set at 188.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.0700; treatment rate λ₁ = 0.1350 events per patient-year; follow-up T = 0.46 years.
2. n = (1.96 + 0.842)² × (1/0.0700 + 1/0.1350) / (0.46 × [ln(1.929)]²) = 858.2, rounded up to 859 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
lambda0 <- 0.07                      # control rate, events per patient-year
lambda1 <- 0.135                      # treatment rate
tt      <- 0.459946339593714                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(5123703)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 859 (80% power), 1,149 (90% power)
 75% of observed effect: n per arm = 1,619 (80% power), 2,167 (90% power)
 50% of observed effect: n per arm = 3,889 (80% power), 5,206 (90% power)
Simulated power, Poisson counts, n = 859 per arm: 0.819
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.641

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor's primary result is an adjusted rate ratio of 0.517, with a 95% confidence interval of 0.193 to 1.329. The registry labels this analysis noninferiority and states that the sponsor assessed ocrelizumab versus fingolimod. The noninferiority margin, primary decision rule, and primary p-value are not reported in the registry record, so the reported label and estimate alone do not establish whether the prespecified noninferiority criterion was met.

The unadjusted re-calculation from the arm-level rates gives a Fingolimod-to-ocrelizumab rate ratio of 1.929 and p = 0.167. That result is not a recalculation of the sponsor's adjusted model. It compares the groups in the reverse direction and does not apply the sponsor's adjustment. Differences between the numbers therefore should not be interpreted as a discrepancy in the trial results. The registry indicates no discrepancy between the posted sponsor analysis and the re-calculation as defined for this record.

The registry also reports an ARR analysis labeled superiority, with a Wald Test, the same adjusted rate-ratio estimate and confidence interval, and p = 0.159. This is distinct in label from the primary noninferiority analysis. The registry record does not explain the relationship between these analyses in enough detail to reconstruct the complete statistical plan. The sponsor's adjusted analysis should be understood as the trial's reported inferential result; the simple unadjusted calculation is supplementary and does not supersede it.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome, protocol-defined ARR, and lists secondary measures that include ARR, MRI lesions, adverse events, pharmacokinetic measures, anti-drug antibodies, and CD19-positive B-cell counts. It also reports a primary analysis labeled noninferiority and a separate ARR analysis labeled superiority. These entries describe multiple inferential questions, but the full statistical testing plan is not reported in the registry record.

Multiplicity arises when several hypotheses or endpoints are tested. General statistical explanation: with repeated testing, the chance of at least one result appearing statistically notable by chance can rise. A prespecified hierarchy, adjustment, or other testing strategy can help define how evidence should be interpreted across outcomes. The registry record does not report whether such a strategy was used, how the primary and secondary tests were ordered, or whether the reported secondary p-value was adjusted. The secondary analyses should therefore be read as less confirmatory than the primary analysis unless further analysis-plan information is available.

The primary analysis is described as an adjusted noninferiority assessment, but the margin and decision rule are not reported. The method details for the primary model, covariate adjustment, and handling of departures from model assumptions are also not reported in the registry record. Although a Wald Test is listed for the secondary ARR analysis, that does not supply the missing details of the primary noninferiority method.

The full analysis set is defined as all randomized participants, grouped according to assigned treatment. This is the only explicit primary analysis-population definition in the record. Details about missing outcome data, exposure-time calculation when follow-up is incomplete, imputation, censoring, sensitivity analyses, and analysis-specific exclusions are not reported in the registry record. These details are relevant to a rate endpoint because the calculation depends on both relapse counts and accumulated patient-years.

The registry's status is active, not recruiting, and its listed primary completion date is 2025-06-09. The record does not describe whether all secondary analyses are complete or whether further results will be posted. The absence of analysis-plan details and secondary numerical results limits assessment of multiplicity, missingness, and the robustness of the reported estimates.

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: pneumonia (2.2%), neutropenia (1.1%), sinus bradycardia (1.1%), general physical health deterioration (1.1%), conjunctivitis (1.1%).

The posted serious adverse event counts are 6 among 93 participants at risk in the ocrelizumab group and 8 among 92 participants at risk in the fingolimod group. The registry reports 0 deaths in each group. Other adverse events are recorded for 76 of 93 participants at risk in the ocrelizumab group and 65 of 92 in the fingolimod group. These are participant counts, not event counts; a participant may have experienced more than one event.

The listed serious adverse event terms include pneumonia (2.2%), neutropenia (1.1%), sinus bradycardia (1.1%), general physical health deterioration (1.1%), conjunctivitis (1.1%), and dengue fever (1.1%). The registry entries do not provide enough information to assess the timing, duration, recurrence, treatment relatedness, or severity distribution of these terms beyond their listing as serious events.

These counts are descriptive and should be interpreted with the group sizes and follow-up context in mind. The registry record does not report a comparative statistical analysis of adverse events, nor does the listed information establish whether an event was caused by a study treatment. Differences in counts alone do not demonstrate a treatment effect on safety.

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

The posted results describe a randomized comparison of ocrelizumab and fingolimod for protocol-defined ARR in children and adolescents with RRMS. The arm-level rates are 0.07 and 0.135 relapses per patient-year, respectively. The adjusted primary rate ratio is reported as 0.517, with a 95% confidence interval of 0.193 to 1.329. The interval includes the equal-rate value and allows a range of relative effects, so the estimate should be read with its uncertainty rather than as a precise treatment difference.

The registry labels the primary analysis noninferiority, but the margin and decision rule required to interpret that objective are not reported in the registry record. The posted estimate therefore cannot establish from the available information whether noninferiority was demonstrated. The separate superiority-labeled ARR analysis reports p = 0.159; a p-value is not the probability that a treatment is effective or ineffective, and it does not establish equivalence.

These data do not determine whether either treatment should be chosen for an individual. They do not show that one treatment works or does not work, and they do not resolve treatment effects on every outcome of interest. The registry lists other efficacy, imaging, safety, pharmacokinetic, and immunogenicity outcomes, but numerical results for most of those measures are not reported in the registry record. A full assessment of those domains is therefore not possible from the posted results.

General statistical explanation: absence of a statistically conclusive difference is not evidence that two treatments are identical. Conversely, an observed numerical difference does not by itself establish a reliable or clinically meaningful difference. Interpretation depends on the endpoint definition, uncertainty, analysis plan, missing-data handling, and clinical context. Several of those details, including the noninferiority margin and missing-data methods, are not reported in the registry record.

The safety counts are also descriptive. They report serious and other adverse-event participants and deaths, but do not establish causality or provide a complete comparative safety analysis. Taken together, the registry supports a cautious statistical reading of the reported ARR estimates, while leaving important questions about the noninferiority criterion and other outcomes unresolved.

18. Why This Trial Matters Statistically

This trial raises statistical issues that are especially visible in randomized comparisons of event rates. ARR is based on relapse counts divided by patient-years, so both event occurrence and exposure time contribute to the estimate. This differs from an endpoint based only on whether each participant experienced an event. The rate-ratio framework matches that structure by comparing rates rather than raw counts alone.

The registry also makes an important distinction between an adjusted primary analysis and a simple unadjusted calculation. The sponsor reports an adjusted rate ratio and labels the primary assessment noninferiority. A summary-statistic re-calculation can help readers understand the posted arm-level rates, but it cannot reproduce the sponsor's model or its adjustments. Keeping these analyses distinct prevents a straightforward calculation from being mistaken for the formal trial result.

Noninferiority analysis requires more than a rate ratio and confidence interval: the margin and decision rule are central to the claim. Their absence from the registry record limits the ability to interpret the stated objective. This is a useful example of why estimates, uncertainty, and design criteria need to be read together rather than treating an analysis label as a conclusion.

The record further illustrates how precision matters. The adjusted interval spans the null value, and the arm-level estimates also have substantial uncertainty. The posted results should therefore be interpreted in terms of the range of effects compatible with the analysis, rather than as definitive evidence of a particular relative effect. Finally, the absence of numerical results for most secondary endpoints and details about multiplicity and missing data limits broader synthesis. Statistical interpretation depends not only on the endpoint estimate but also on transparency about the analysis plan and the evidence across outcomes.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record does not report the noninferiority margin or the formal decision rule for the primary analysis. Without those elements, the label of noninferiority cannot be translated into a conclusion about whether the criterion was met. The adjusted model's detailed specification and covariates are also not reported, limiting independent evaluation or reproduction of the sponsor's estimate.

The primary outcome depends on protocol-defined relapse events and accumulated patient-years. The definition is detailed, but the record does not report adjudication procedures, missing relapse assessments, how incomplete follow-up contributed to exposure time, or sensitivity analyses. These omissions limit assessment of the robustness of the rate estimate. The registry also does not report whether over-dispersion was evaluated or how it was addressed in the primary analysis.

Numerical results for most listed secondary outcomes are not reported in the registry record. As a result, the broader pattern across MRI, safety, pharmacokinetic, immunogenicity, and CD19-positive B-cell measures cannot be assessed. The record does not report a multiplicity strategy for the multiple outcomes and analyses, or enough detail to determine how secondary tests were interpreted relative to the primary objective.

The registry lists enrollment of 188 but reports primary endpoint arm sizes of 93 and 94. The record does not explain the difference between enrollment and the endpoint analysis counts. It defines the full analysis set as all randomized participants, but does not give further detail about missing data or analysis-specific exclusions. The study status is active, not recruiting, and the listed primary completion date does not by itself establish that all analyses or follow-up are complete. These limitations concern what is documented in the registry and should not be treated as evidence that a particular method was or was not used outside the record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate Safety and Efficacy of Ocrelizumab in Comparison With Fingolimod in Children and Adolescents With Relapsing-remitting Multiple Sclerosis (RRMS) — NCT05123703.
• Registry record last updated 2026-07-15; status last verified 2026-07.
• Results first posted 2026-07-15.
• 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

NCT05123703 is a randomized, quadruple-masked, parallel-group Phase III study sponsored by Hoffmann-La Roche. It compares ocrelizumab with fingolimod in children and adolescents aged 10 to < 18 years with RRMS. The registry lists enrollment of 188 and status active, not recruiting.

The primary outcome is protocol-defined ARR, reported in relapses per patient-year. The arm-level estimates are 0.07 for ocrelizumab and 0.135 for fingolimod. The sponsor's adjusted rate ratio is 0.517, with a 95% confidence interval of 0.193 to 1.329, and is labeled a noninferiority analysis. The margin and decision rule are not reported in the registry record.

The registry lists secondary efficacy, imaging, safety, pharmacokinetic, immunogenicity, and blood-cell measures, but numerical results for most are not reported in the registry record. Serious adverse event counts are 6 of 93 for ocrelizumab and 8 of 92 for fingolimod; deaths are reported as 0 in each group. Missing-data methods, the original sample-size justification, and a multiplicity strategy are not reported in the registry record.