Dose-finding Study for SAR442168 in Relapsing Multiple Sclerosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose-finding Study for SAR442168 in Relapsing Multiple Sclerosis (NCT03889639), a randomized phase 2 study. The primary outcome is Brain Magnetic Resonance Imaging (MRI) Assessment: Number of New Gadolinium (Gd) Enhancing T1-hyperintense Lesions.

2. Clinical Question

The endpoint was measured at different calendar study weeks according to cohort: at Week 12 for Cohort 1 participants receiving SAR442168 and at Week 16 for Cohort 2 participants after their placebo period. Cohort 2 placebo observations were assessed at Week 4. This timing matters when interpreting the pooled dose groups and placebo comparator: they represent treatment-period observations at different points in the crossover schedules, not a single concurrent assessment for every participant.

3. Trial Design

The registry describes NCT03889639 as a randomized, double-masked, phase 2b dose-finding study using a crossover model. The study enrolled 130 participants with relapsing multiple sclerosis and is recorded as completed. The registry lists Sanofi as the sponsor. The recorded study start was 2019-03-29 and primary completion was 2020-01-02.

Four SAR442168 doses were evaluated: 5 mg, 15 mg, 30 mg, and 60 mg. The crossover schedules differed by cohort. Cohort 1 received SAR442168 for the first 12 weeks and then matching placebo for 4 weeks. Cohort 2 received placebo for the first 4 weeks and then SAR442168 for 12 weeks. The primary outcome description states that the dose results pooled participants from Cohorts 1 and 2 at each dose, while the placebo result was pooled from Cohort 2. Placebo administration in Cohort 1 was not planned as a source of primary endpoint data.

This design means that the placebo observations and the SAR442168 observations were collected at different points in the scheduled treatment periods. The record states that the primary outcome was assessed after 12 weeks of SAR442168 treatment for the active-treatment groups and at Week 4 for Cohort 2 placebo. It does not report enough detail to establish how any possible period or sequence effects were handled in the sponsor’s model.

Primary analysis was described as using a modified intent-to-treat population: randomized participants exposed to study drug, analyzed according to the treatment assigned by randomization. The record reports group-level evaluable counts for the primary endpoint. Details of the original sample-size justification, randomization procedure, masking implementation, or the 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: A total of 130 participants were randomized and treated in this study. Participants were centrally assigned to 1 of 8 arms (4 dose groups at an equal ratio to start with SAR442168 \[all considered as Cohort 1\] or placebo \[all considered as Cohort 2\]).

Only the first 6 of 8 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on modified intent-to-treat (mITT) population that included all randomly assigned participants exposed to the study drug, analyzed according to the treatment assigned by randomization. Here, 'Overall number of participants analyzed' signifies number of participants evaluable for this outcome measure.

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 analysis was performed on randomized population that included any participant who had been allocated to a randomly assigned treatment, regardless of whether the treatment kit was used.

Only the first 6 of 9 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Brain Magnetic Resonance Imaging (MRI) Assessment: Number of New Gadolinium (Gd) Enhancing T1-hyperintense Lesions, measured over After 12 weeks of SAR442168 treatment for SAR442168 reporting arms (i.e., at Week 12 for Cohort 1 participants, at Week 16 for Cohort 2 participants) and at Week 4 for Cohort 2 placebo.

The primary endpoint is the number of new gadolinium-enhancing T1-hyperintense lesions detected by brain MRI. Gadolinium enhancement on MRI is used in this trial as an imaging indicator of active brain lesions. The endpoint counts new lesions over the specified treatment period; it does not directly measure a participant’s symptoms, functioning, or long-term clinical course.

The registry reports the endpoint as a mean with a standard deviation. Lesion counts are count data and can be unevenly distributed: many observations may be small while a smaller number are much larger. For that reason, the sponsor’s reported comparison used negative binomial regression, a model suited to count outcomes that can accommodate greater variability than a basic Poisson model. This is a general statistical rationale; the record does not provide diagnostic information about the observed distribution or model fit.

The timing of the MRI measurement is part of the endpoint definition. SAR442168 results were assessed after 12 weeks of active treatment, at Week 12 in Cohort 1 and Week 16 in Cohort 2. The Cohort 2 placebo assessment was at Week 4. Consequently, the comparison is based on the registry’s pooled treatment-period groups and the specified placebo observations, rather than on a single common assessment week across all arms.

The endpoint was chosen to address the study’s stated primary objective: evaluating the dose-response relationship for reducing the number of new active brain lesions. It is an imaging outcome for this dose-finding study. The registry’s primary endpoint alone cannot establish effects on outcomes that were not measured by this endpoint.

7. Results Posted in the Registry

• Cohorts 1 and 2: SAR442168 5 mg: mean 1.39 versus 1.03 on control; difference 0.36 (95% CI -0.93 to 1.65), standardized effect d = 0.13; z-test p = 0.586.
• Cohorts 1 and 2: SAR442168 15 mg: mean 0.77 versus 1.03 on control; difference -0.26 (95% CI -1.08 to 0.56), standardized effect d = -0.12; z-test p = 0.536.
• Cohorts 1 and 2: SAR442168 30 mg: mean 0.76 versus 1.03 on control; difference -0.27 (95% CI -1.57 to 1.03), standardized effect d = -0.10; z-test p = 0.683.
• Cohorts 1 and 2: SAR442168 60 mg: mean 0.13 versus 1.03 on control; difference -0.90 (95% CI -1.56 to -0.24), standardized effect d = -0.44; z-test p = 0.007.

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.

Number of New or Enlarging T2 Lesions

• 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 deviations.
• Result:
  • Cohorts 1 and 2: SAR442168 5 mg: mean 1.90 versus 2.12 on control; difference -0.22 (95% CI -2.14 to 1.70), standardized effect d = -0.05; z-test p = 0.822.
  • Cohorts 1 and 2: SAR442168 15 mg: mean 1.32 versus 2.12 on control; difference -0.80 (95% CI -2.27 to 0.67), standardized effect d = -0.19; z-test p = 0.285.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohorts 1 and 2: SAR442168 5 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohorts 1 and 2: SAR442168 15 mg and the control. The interval gives the range of effects that remain compatible with the data.

Total Number of Gd-enhancing T1-hyperintense Lesions

• 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 deviations.
• Result:
  • Cohorts 1 and 2: SAR442168 5 mg: mean 1.77 versus 1.36 on control; difference 0.41 (95% CI -1.29 to 2.11), standardized effect d = 0.11; z-test p = 0.636.
  • Cohorts 1 and 2: SAR442168 15 mg: mean 0.87 versus 1.36 on control; difference -0.49 (95% CI -1.55 to 0.57), standardized effect d = -0.16; z-test p = 0.364.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohorts 1 and 2: SAR442168 5 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohorts 1 and 2: SAR442168 15 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the imaging assessment to new or enlarging T2 lesions and total gadolinium-enhancing T1-hyperintense lesions, alongside adverse-event and laboratory, vital-sign, and ECG measures. Across the posted lesion-count summaries, the pattern is not uniformly dose-ordered: group means vary across doses and outcome definitions. The 60 mg groups tend to have lower posted lesion means than pooled placebo in the available summaries, but this descriptive pattern is not itself a substitute for a prespecified model-based comparison.

The reported secondary model analyses are limited in the registry record. For new or enlarging T2 lesions, sponsor-reported comparisons are listed for 5 mg and 15 mg; for total gadolinium-enhancing lesions, comparisons are also listed for those doses. The corresponding reported confidence intervals include no relative reduction, and the p-values do not provide clear evidence of a difference in those listed comparisons. The record does not show a complete set of model-based comparisons for every dose and secondary endpoint.

Secondary findings provide context for the primary MRI result but should carry less inferential weight. These endpoints are additional questions beyond the primary outcome, and testing several outcomes or dose comparisons increases the chance of apparently notable results arising by chance. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Accordingly, the secondary results are best treated as supportive or exploratory evidence rather than independent confirmation of the primary finding.

The secondary outcomes also differ in measurement and analysis. Lesion counts are imaging measures, whereas adverse events and laboratory or ECG abnormalities describe safety observations. Their interpretation depends on their own definitions, assessment periods, and analysis populations. The registry lists those outcome categories, but complete numerical results and analysis details are not reported for every listed measure.

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

• Number of New or Enlarging T2 Lesions
• Total Number of Gd-enhancing T1-hyperintense Lesions
• Number of Participants With Treatment-emergent Adverse Events (TEAEs) and Treatment-emergent Serious Adverse Events (TESAEs): Weeks 1-4 Period
• Number of Participants With Treatment-emergent Adverse Events and Treatment-emergent Serious Adverse Events: SAR442168 Treatment Period
• Number of Participants With Individual Clinically Relevant Abnormalities in Laboratory Tests (Hematology, Chemistry, Urinalysis), Vital Signs, and Electrocardiograms (ECG)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a negative binomial regression model for the primary comparisons. This is a model for counts, such as the number of lesions. As a general statistical explanation, count outcomes often have a right-skewed distribution: many observations may be low, with some much higher counts. A Poisson model assumes that the mean and variance are linked in a relatively restrictive way. When counts vary more than that assumption allows, over-dispersion can make standard errors too small if it is ignored. A negative binomial model allows additional variability. The registry does not report model diagnostics or the estimated over-dispersion parameter, so the adequacy of the fit cannot be assessed from the record.

What is the model estimating?

The sponsor’s results are expressed as relative reduction in lesions, with a point estimate, 95% confidence interval, and p-value for each dose compared with pooled Cohort 2 placebo. The analysis is labeled as a superiority comparison. The registry does not explain the model’s exact parameterization, covariates, offset, or sign convention. Therefore, the reported estimates should be quoted as the registry gives them rather than attempting to reconstruct the model from the arm means.

For example, the sponsor reports a relative reduction of 85.02% for 60 mg, with a 95% confidence interval from 28.02% to 96.88%. By contrast, simple recalculations from the posted summary statistics compare arithmetic means. A mean difference is a subtraction of the posted group means, while the standard error and confidence interval in such a recalculation use the group standard deviations and sample sizes. This calculation is unadjusted and does not account for the count distribution or any covariates that may have entered the sponsor’s model.

What does a confidence interval express?

In general, a confidence interval describes the range of effect values reasonably compatible with the data and the statistical model at the stated confidence level. A narrow interval indicates greater precision than a wide interval, all else equal. An interval that includes zero for a difference, or no reduction for a relative-reduction measure, indicates that the data are compatible with no difference under that model. It does not prove that the true effect is exactly zero. The sponsor’s primary intervals are 95% intervals; the recalculated intervals are also presented as 95% intervals.

What does a p-value express?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The registry gives p-values for the sponsor’s comparisons and unadjusted p-values for the simple recalculations. The record does not report a multiplicity adjustment, so the stated values should not be read as if they necessarily account for testing several doses.

The simple recalculations are based on the posted arm means, standard deviations, and evaluable counts. For the primary outcome, these recalculations produce mean differences and confidence intervals for each dose against pooled placebo. They are useful as a transparent comparison of the summaries, but they do not reproduce the sponsor’s negative binomial regression. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence for the trial’s primary inference.

The crossover structure also matters methodologically. Participants received placebo and active treatment in a sequence that differed by cohort, and the reported endpoint timing differed between the cohorts. The registry does not report whether the primary model included cohort, period, sequence, or participant-level effects, nor whether any carryover assessment was conducted. Those details are not reported in the registry record and should not be assumed.

The analysis population is described as modified intent-to-treat and includes randomized participants exposed to study drug, analyzed according to randomized assignment. The record defines the primary outcome’s analyzed count as the number of participants evaluable for that outcome, but does not give the full rules for evaluability or explain how missing MRI assessments were handled. The reported methods therefore allow identification of the broad analysis population and model family, but not a complete independent reconstruction of the sponsor’s analysis.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for 60 mg runs from 28.02% to 96.88% relative reduction in lesions. It excludes zero, while still spanning a broad range of possible reduction magnitudes. This supports a model-based difference from pooled placebo in this comparison, but the interval’s width means that the exact size of the reduction is not pinned down precisely.

The other sponsor-reported primary intervals are much less decisive: each includes zero. Their ranges are also broad, extending from negative estimates to positive reductions. Such intervals reflect uncertainty about both the direction and magnitude of those comparisons under the reported model. They do not establish that the true effects are absent.

The group-level data also show notable spread. For example, in the 60 mg arm the mean was 0.13 lesions and the standard deviation was 0.43; in pooled placebo the mean was 1.03 and the standard deviation was 2.5. Counts with substantial variation can make estimates sensitive to a small number of larger observations, which is one reason the negative binomial model is relevant as a general approach. The registry does not provide individual-level data or model diagnostics to assess that sensitivity directly.

The simple mean-difference interval for 60 mg is -1.556 to -0.244 lesions, while the sponsor’s interval is on a relative-reduction scale. These are different estimands from different analyses, so their precision and values should not be compared as though they were the same calculation. The posted discrepancy further argues against treating the recalculated interval as a replacement for the sponsor’s model-based estimate.

In general, confidence intervals communicate statistical precision, not the probability that a specific result will be replicated. They also do not address unreported sources of uncertainty, such as analysis choices, missing observations, or multiple testing. The registry does not report a multiplicity-adjusted interval or an analysis accounting for the crossover structure in sufficient detail to evaluate those issues.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations give participants per arm for the continuous-outcome recalculations; they are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each illustration, the effect to detect is the stated fraction of the observed effect. These are planning calculations based on the observed effect, not the original design assumptions of the trial. The trial’s own original sample-size assumptions 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 to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column describes the corresponding number for a higher chance of detection. These are prospective planning interpretations of the calculation, not evidence about what the completed trial’s chance of detecting an effect was.

Rows using 100%, 75%, or 50% of an observed effect represent different assumed effect sizes. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants per arm to detect it at the same power and significance level. The figures can therefore increase sharply as the target effect becomes smaller.

These calculations are not observed power. They are sample-size planning illustrations derived from the observed summary effect, under the stated assumptions. They do not establish that a study was adequately or inadequately designed, and they do not replace the sponsor’s analysis or the trial’s unavailable original design justification. The calculations also use a normal approximation for the mean-difference summaries, whereas the sponsor’s primary analysis used negative binomial regression for lesion counts.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.360; pooled standard deviation σ = 2.759.
2. n = 2 × (1.96 + 0.842)² × 2.759² / 0.360² = 921.8, rounded up to 922 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
delta <- 0.36                      # observed difference in means
sigma <- 2.75866403766883                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3889639)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 922 (80% power), 1,235 (90% power)
 75% of observed effect: n per arm = 1,639 (80% power), 2,194 (90% power)
 50% of observed effect: n per arm = 3,688 (80% power), 4,937 (90% power)
power.t.test: 922.7 
Simulated power at n = 922 per arm: 0.802 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s analysis is the negative binomial regression comparison reported in the registry. It is the primary source for interpreting the trial’s planned count outcome. In particular, the sponsor reports an 85.02% relative reduction for SAR442168 60 mg compared with pooled Cohort 2 placebo, with a 95% confidence interval from 28.02% to 96.88% and p = 0.018. The lower-dose estimates and intervals are also reported, but their intervals include zero.

The recalculation uses the posted group means and standard deviations to estimate unadjusted differences in mean lesion counts. For 60 mg, it gives a mean difference of -0.9 lesions, a 95% confidence interval from -1.556 to -0.244, and an unadjusted p-value of 0.007. This calculation is not the same model or estimand as the sponsor’s relative-reduction analysis. It cannot account for model details that are not available in the group summaries.

The registry flags a discrepancy between the sponsor’s analysis and the recalculation. Under that circumstance, the sponsor’s own analysis takes precedence. The recalculation can help readers understand the direction and scale of the posted means, but it should not be presented as a correction to, or replacement for, the sponsor-reported result. The registry record does not provide enough methodological detail to determine the source of the discrepancy.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is compared across four SAR442168 doses against pooled placebo. That creates multiple dose comparisons even before considering the secondary imaging and safety outcomes. The registry reports p-values and confidence intervals for the primary comparisons, but does not report whether the sponsor used a family-wise error adjustment, a hierarchical testing procedure, or another method to control multiplicity. It also does not report a prespecified order for interpreting the dose comparisons. The 60 mg result should therefore be read as the reported comparison, with the multiplicity handling not reported in the registry record.

The record lists multiple secondary outcomes, including additional lesion counts, adverse events, and clinically relevant laboratory, vital-sign, and ECG abnormalities. It does not explain how many secondary hypotheses were formally tested, whether those tests were confirmatory, or how their p-values were adjusted. An unadjusted secondary p-value, where reported, does not account for the broader set of possible comparisons and should be interpreted cautiously.

Missing-data procedures are also not reported in sufficient detail. The primary analysis description identifies a modified intent-to-treat population of randomized participants exposed to study drug and states that the analyzed number refers to participants evaluable for the outcome. However, the registry does not give the criteria for evaluability, the number of missing MRI assessments, reasons for missingness, or the method used to handle missing outcome data. It is therefore not possible to assess from the record whether missingness could have affected the comparisons.

The crossover design makes additional analysis details relevant. The cohorts received placebo and active treatment in a different order, and their endpoint assessments occurred at different study weeks. Whether period, sequence, or participant effects were incorporated into the sponsor’s analysis is not reported in the registry record. Nor does the record state whether possible carryover effects were evaluated. These omissions limit the ability to independently assess how the crossover design informed the model.

The registry also does not report the full statistical analysis plan, model diagnostics, covariate specification, or a sample-size justification. These are reporting limitations, not evidence that the analyses were necessarily inappropriate. They do, however, constrain independent evaluation of multiplicity, missingness, and the robustness of the reported results.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: multiple sclerosis relapse (3.1%).

The registry reports serious adverse events by treatment group and gives the number at risk and the number affected. No deaths are listed in any of the reported groups. One serious adverse event is reported in the 60 mg SAR442168 group; the other listed active-dose groups and both pooled placebo groups report none. The leading serious-event term listed in the record is multiple sclerosis relapse, at 3.1%. The record does not identify that percentage with a particular dose group.

These are descriptive safety counts over the recorded treatment periods. They should be interpreted with the group sizes and exposure periods in mind: the crossover cohorts received placebo and active treatment for different durations and in a different sequence. The registry lists separate pooled placebo groups for Cohort 1 and Cohort 2 as well as dose groups, so those categories are not interchangeable. The reported counts alone do not establish a comparative safety effect.

The record also lists participants with other treatment-emergent adverse events, but the serious-event figures above refer only to serious adverse events. Complete details of event types, timing, severity, exposure-adjusted rates, and statistical comparisons are not reported in the registry record. These summaries describe what was recorded in this study and are not a basis for individual medical decisions.

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

The central statistical result is that the sponsor’s negative binomial analysis reports a reduction in new gadolinium-enhancing lesions for the 60 mg comparison against pooled Cohort 2 placebo, with a 95% confidence interval that excludes zero. The lower-dose comparisons have confidence intervals that include zero. The simple recalculation from means points in a similar direction for 60 mg, but it is not the same analysis and does not supersede the sponsor’s result because the registry flags a discrepancy.

This conclusion is specific to the primary MRI lesion-count endpoint, the treatment and assessment periods described in the registry, and the sponsor’s reported model. It does not show that the same pattern applies to every imaging measure, to symptoms, or to outcomes over a longer period. The study’s stated secondary objectives included imaging efficacy measures and safety and tolerability, but the primary result is not a complete account of those objectives.

A confidence interval describes uncertainty in the estimate under the model; it does not guarantee that a future study will reproduce the same estimate. The wide intervals for several comparisons indicate uncertainty about their effect sizes. The 60 mg interval is compatible with a range of reductions, rather than one exact value. The registry does not report multiplicity adjustment, missing-data methods, or sufficient crossover-model details to resolve those sources of uncertainty.

The study was designed as a dose-finding investigation and used a particular crossover schedule. It should not be interpreted as a direct test of long-term clinical outcomes or as proof of the effect of SAR442168 in other populations or settings. The registry record supports a description of the observed and modeled MRI findings in this trial; broader conclusions are not established by these results alone.

18. Why This Trial Matters Statistically

Dose-finding trials raise a statistical question beyond whether one comparison differs from a control: they aim to characterize how outcomes vary across doses. The primary objective in this study was to determine the dose-response relationship for SAR442168 on new active brain lesions. The reported results make it possible to distinguish the sponsor’s model-based estimate at each dose from descriptive group means, an important separation when the endpoint is a variable count.

The trial also illustrates why an analysis model matters. The sponsor used negative binomial regression for lesion counts, while a simple recalculation from posted means treats the outcome as a continuous measure and produces a different estimand. Both can describe aspects of the data, but they answer different statistical questions. The registry flags a discrepancy, so reporting the sponsor analysis as primary avoids mistaking a summary-statistic calculation for the trial’s own model.

The crossover structure and differing endpoint timing are also relevant to interpretation. Placebo and active-treatment observations were collected at distinct points in the cohorts’ schedules. Knowing those details helps readers ask whether period, sequence, and participant effects were accounted for, while recognizing that the registry does not report the full model specification.

Finally, multiple doses and outcomes make multiplicity and reporting completeness important. The registry offers a useful record of the primary outcome, secondary outcome categories, and safety counts, but does not report several details needed for a complete independent statistical assessment. This makes the distinction between a reported signal, its precision, and the limitations of what can be inferred especially important.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific limitations constrain interpretation. First, the crossover schedules were not identical: Cohort 1 received SAR442168 before placebo, while Cohort 2 received placebo before SAR442168. Primary measurements were made at different study weeks, and the primary placebo data came from Cohort 2. The registry does not report whether the analysis adjusted for cohort, sequence, period, or within-participant effects, or whether carryover was evaluated.

Second, the sponsor’s primary endpoint analysis uses negative binomial regression, but the model specification is not reported in full. Covariates, handling of exposure time, fit diagnostics, and sensitivity analyses are not described. The discrepancy flag indicates that simple recalculations from posted summary statistics do not fully match the sponsor’s analysis. The sponsor’s own model-based result takes precedence, but the source of the discrepancy is not reported.

Third, the record does not report multiplicity procedures for the dose comparisons and secondary endpoints. The number of questions considered makes unadjusted secondary results less persuasive as confirmatory evidence. Missing-data handling is also not reported: the primary population is described as modified intent-to-treat and evaluable, but the rules for evaluability, missing MRI assessments, and their treatment in the analysis are absent.

Finally, the primary outcome is an MRI lesion count measured over a defined treatment period. The result does not directly represent symptoms or longer-term outcomes. The registry’s safety summary is descriptive and does not provide exposure-adjusted comparisons or the full detail needed to assess event timing and severity. These are limits on what can be concluded from the registry record, rather than claims about unreported aspects of trial conduct.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose-finding Study for SAR442168 in Relapsing Multiple Sclerosis — NCT03889639.
• Registry record last updated 2025-09-17; status last verified 2025-09.
• Results first posted 2023-03-08.
• 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

NCT03889639 is a completed, randomized, double-masked, phase 2b crossover dose-finding study of SAR442168 in relapsing multiple sclerosis. The registry reports enrollment of 130 participants and comparisons of 5 mg, 15 mg, 30 mg, and 60 mg with pooled Cohort 2 placebo for the primary MRI lesion-count outcome.

The sponsor’s negative binomial regression reports a 85.02% relative reduction for 60 mg, with a 95% confidence interval from 28.02% to 96.88% and p = 0.018. The other reported primary comparisons have confidence intervals that include zero. The registry flags a discrepancy with simple recalculations from posted summary statistics; the sponsor’s own analysis takes precedence.

Interpretation is limited by unreported details of multiplicity, missing-data handling, and crossover-model specification. The primary finding concerns the recorded MRI endpoint and should not be extended to unmeasured outcomes.