A Phase 2 Study to Evaluate the Safety and Efficacy of LOU064 in Patients With Moderate to Severe Sjögren's Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 2 Study to Evaluate the Safety and Efficacy of LOU064 in Patients With Moderate to Severe Sjögren's Syndrome (NCT04035668), a randomized phase 2 study. The primary outcome is Change From Baseline in EULAR Sjögren's Syndrome Disease Activity Index (ESSDAI) Total Score at Week 24.

2. Clinical Question

The primary endpoint was change from baseline in the EULAR Sjögren's Syndrome Disease Activity Index (ESSDAI) total score at Week 24. The registry reports a model-based comparison of any remibrutinib with placebo, alongside results for the two dose groups and a comparison between the dose groups. Negative change indicates improvement on this measure, because higher ESSDAI scores indicate more disease activity.

The study record describes an adaptive Phase 2 study intended to evaluate safety and efficacy and characterize dose-response. The record does not report the specific decision rules or adaptations used. The clinical question is therefore about the posted Week 24 estimates and their precision, not about unreported adaptive-design decisions or a definitive treatment conclusion.

3. Trial Design

NCT04035668 is a Phase 2 randomized, triple-masked, parallel-group, placebo-controlled study of LOU064, identified in the registry as remibrutinib. The official title describes a multicenter study in participants with moderate to severe Sjögren's syndrome. The registry lists Novartis Pharmaceuticals as sponsor. Enrollment was 73, and the recorded status is terminated. The study started on 2019-07-12, with primary completion on 2021-11-23. The reason for termination is not reported in the registry record.

The intervention groups were remibrutinib 100 mg once daily, remibrutinib 100 mg twice daily, and placebo. The primary outcome analysis also includes a combined any-remibrutinib group. The primary analysis population is described as randomized participants in the Full Analysis Set who had a valid assessment for the outcome. The arm counts for the primary endpoint are 24 for each dose group and 24 for placebo; the combined remibrutinib group has 48 participants.

The study is described as adaptive, but the protocol details for any adaptations, allocation procedures, or dose-selection rules are not reported in the registry record. The original sample-size target and its justification, including the assumptions used in planning the trial, are also not reported. The record identifies triple masking but does not describe which parties were masked. These omissions limit what can be inferred about the design decisions beyond the listed randomization, masking, parallel groups, and placebo comparison.

The planned outcomes extend beyond ESSDAI, including patient-reported symptoms, fatigue, health status, physician assessment, adverse events, and remibrutinib blood concentrations. The record lists 17 outcome measures and 70 analyses. Study status and outcome reporting should be read as registry information; the reason for termination and any broader account of study conduct 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: The screening period of up to 6 weeks began after the subject had provided written informed consent. Eligible subjects were randomized in a 1:1:1 ratio to one of the 3 treatment groups.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in the Full Analysis Set (FAS) with a valid assessment for the outcome measure. FAS included all participants who were randomized in the study.

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.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in EULAR Sjögren's Syndrome Disease Activity Index (ESSDAI) Total Score at Week 24, measured over Baseline, Week 24.

The primary endpoint is change from baseline in the ESSDAI total score at Week 24. ESSDAI is a validated disease activity measure for Sjögren's syndrome. It combines scores across 12 organ-specific domains: constitutional, lymphadenopathy, glandular, articular, cutaneous, pulmonary, renal, muscular, peripheral nervous system, central nervous system, hematological, and biological. Domain scores reflect the severity of disease activity features and are combined using weights. The total score ranges from 0 to 123, with higher scores indicating more disease activity.

A change below zero means the score declined from baseline; the registry describes a negative change as improvement. The endpoint captures activity across several domains rather than focusing on a single symptom or organ. That makes it relevant to a study asking about overall disease activity, while also meaning that the total score compresses information from different domains into one measure. The registry does not report domain-specific primary analyses in the registry record described for this result.

Baseline is defined as the last assessment before the first dose of study treatment. The Week 24 outcome is estimated using a mixed effect model for repeated measurements fitted to post-baseline changes through Week 24. The reported arm values are least-squares means with standard errors, so they are model estimates rather than simple raw averages. The registry specifies a Full Analysis Set population consisting of randomized participants with a valid assessment for this outcome.

7. Results Posted in the Registry

• Remibrutinib 100 mg qd: mean -4.70 versus -1.34 on control; difference -3.36 (95% CI -5.47 to -1.25), standardized effect d = -0.90; z-test p = 0.002.
• Remibrutinib 100 mg Bid: mean -3.70 versus -1.34 on control; difference -2.36 (95% CI -4.50 to -0.22), standardized effect d = -0.63; z-test p = 0.030.
• Any Remibrutinib: mean -4.20 versus -1.34 on control; difference -2.86 (95% CI -4.68 to -1.04), standardized effect d = -0.75; z-test p = 0.002.

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.

Maximum Observed Blood Concentration (Cmax) of Remibrutinib at Week 4

• 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:
  • Remibrutinib 100 mg qd: mean 225.00 versus 183.00 on control; difference 42.00 (95% CI -50.96 to 134.96), standardized effect d = 0.35; z-test p = 0.376.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Remibrutinib 100 mg qd and the control. The interval gives the range of effects that remain compatible with the data.

Maximum Observed Blood Concentration (Cmax) of Remibrutinib at Week 24

• 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:
  • Remibrutinib 100 mg qd: mean 169.00 versus 224.00 on control; difference -55.00 (95% CI -171.31 to 61.31), standardized effect d = -0.34; z-test p = 0.354.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Remibrutinib 100 mg qd and the control. The interval gives the range of effects that remain compatible with the data.

Area Under the Blood Concentration-time Curve From Time Zero to 4 Hours Post-dose (AUC0-4h) of Remibrutinib at Week 4

• 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:
  • Remibrutinib 100 mg qd: mean 393.00 versus 351.00 on control; difference 42.00 (95% CI -97.71 to 181.71), standardized effect d = 0.22; z-test p = 0.556.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Remibrutinib 100 mg qd and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary outcomes covering disease activity over time, patient-reported symptom burden, fatigue, health status, physician global assessment, adverse events, and remibrutinib blood concentrations. It lists 17 outcome measures, with 16 secondary outcomes posted. The breadth of these measures reflects different aspects of disease activity, participant experience, safety, and drug exposure; they do not all answer the same question as the primary Week 24 ESSDAI comparison.

The posted pharmacokinetic summaries include maximum observed blood concentration at Week 4 and Week 24, and area under the blood concentration-time curve from time zero to four hours post-dose at Week 4. Their reported dose comparisons have confidence intervals that include zero and unadjusted p-values of 0.376, 0.354, and 0.556, respectively. These outcomes concern blood exposure, not the primary disease-activity endpoint. The registry also names additional secondary outcomes, but the registry entries summarized for this analysis do not give numerical results for all of them. A complete overall direction across all secondary measures cannot be established from the information.

Secondary outcomes can add context to a primary result, but they should not be treated as independent confirmation without considering the number of outcomes and analyses examined. The registry lists 70 analyses, and the multiplicity strategy is not reported in the registry record. When many outcomes are tested, unadjusted results are more vulnerable to chance findings. Secondary results are therefore best viewed as exploratory unless the analysis plan and multiplicity control establish otherwise. They should not override the prespecified primary comparison or be combined into a broad efficacy claim without a stated method.

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

• Change From Baseline in ESSDAI Total Score Over Time
• Change From Baseline in EULAR Sjögren's Syndrome Patient Reported Index (ESSPRI) Total Score Over Time
• Change From Baseline in Functional Assessment of Chronic Illness Therapy-Fatigue Scale (FACIT-F) Total Score Over Time
• Change From Baseline in EuroQual 5 Dimensions (EQ-5D) VAS Score Over Time
• Change From Baseline in Physician Global Assessment Scale (PhGA) Score Over Time
• Number of Participants With Treatment-Emergent Adverse Events (TEAEs) and Serious TEAEs
• Maximum Observed Blood Concentration (Cmax) of Remibrutinib at Week 4
• Maximum Observed Blood Concentration (Cmax) of Remibrutinib at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: change in ESSDAI total score. A continuous outcome retains the amount of change on a scale, rather than reducing results to categories such as improved or not improved. The registered unit is a score on the ESSDAI scale. Since higher ESSDAI values indicate more disease activity, negative change indicates a decline in measured activity from baseline.

What does the MMRM estimate?

The registry says that a mixed effect model for repeated measurements (MMRM) was fitted to changes from baseline for all post-baseline time points through Week 24. In general, a repeated-measures model uses observations from multiple visits and accounts for the fact that measurements from the same participant are related. It can estimate group means and contrasts while using the available repeated outcome data under the model’s assumptions. The registry presents least-squares means, which are model-based group estimates, and standard errors, which describe the estimated uncertainty of those means.

The registry record does not report the model’s covariance structure, fixed-effect terms, degrees-of-freedom method, or detailed missing-data assumptions. Those details should not be inferred from the acronym MMRM alone. The population is specified as randomized participants in the Full Analysis Set with a valid assessment for the endpoint. The handling of participants who lacked an assessment, and the amount or pattern of missing data, are not reported in the registry record.

How should a mean difference be read?

A mean difference compares the estimated mean change in one group with the estimated mean change in another. For the reported any-remibrutinib comparison, the estimate is -2.86 points, using the registry’s stated group order of remibrutinib versus placebo. A negative difference means the estimated change is more negative in the remibrutinib group. The comparison is different from looking at either group’s change in isolation: it uses the placebo group as the reference for interpreting the treatment-group change.

The primary estimates are model-based. The supplementary recalculation uses posted summary statistics and is a simple unadjusted comparison, not an attempt to reproduce the fitted MMRM. For that recalculation, the standard deviations are approximate values inferred from the reported standard errors and group sizes. In general, a simplified recalculation may not reproduce a model-based result because it does not use the repeated-measures structure or the same model adjustments. In this record the discrepancy flag is true, so the sponsor’s own analysis takes precedence.

What do p-values and confidence intervals convey?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the analysis assumptions; it is not the probability that the null hypothesis is true and does not measure clinical importance. The registry reports p = 0.002 for the primary any-remibrutinib comparison. That is the sponsor-reported result for the MMRM contrast. It should be interpreted in the context of the analysis plan and any multiplicity procedures, which are not reported in the registry record.

In general, a confidence interval gives a range of values compatible with the data and the analysis procedure at its stated confidence level. The primary comparison’s reported 95% interval is -4.71 to -1.01. Its width conveys uncertainty about the magnitude of the contrast, while its location gives the direction of the estimated difference. A confidence interval is not a guarantee that the true value lies within the particular interval, and it does not capture uncertainties arising from unreported design or analysis choices.

Why does over-dispersion matter?

General explanation: over-dispersion occurs when variability in data is greater than a model assumes. It can make standard errors and interval estimates too small if the model does not account for that extra variability. The primary endpoint is continuous and analyzed using MMRM, but the registry entries do not identify over-dispersion as a concern or report a diagnostic assessment. It should not be asserted as a specific problem in this trial.

What is known about the analysis population?

The registry defines the primary outcome population as the Full Analysis Set, including all participants randomized in the study, who also had a valid assessment for the outcome measure. That valid-assessment qualification matters: the population described for the posted endpoint is not simply every randomized participant regardless of whether an outcome was available. The record does not state how many randomized participants lacked a valid Week 24 assessment, how missing values were handled, or whether sensitivity analyses were conducted.

11. Confidence Intervals and Precision

The sponsor-reported primary comparison is -2.86 points, with a 95% confidence interval from -4.71 to -1.01. The interval lies below zero, giving a consistent negative direction across its endpoints under the reported MMRM analysis. Its span also shows that the estimate is not a single precisely known value: the data are compatible with a range of magnitudes. The interval should be read as uncertainty around the group contrast, not as a prediction for every participant or a statement about individual response.

The simple recalculation gives -2.86 with a 95% confidence interval from -4.679 to -1.041. The closeness of the point estimates and the modest differences between interval endpoints do not make the calculations interchangeable. The sponsor’s result comes from the MMRM, while the recalculation is an unadjusted summary-statistic comparison. Because the discrepancy flag is true, the sponsor’s analysis takes precedence.

The dose-specific sponsor analysis comparing the two remibrutinib groups has a 95% confidence interval from -3.24 to 1.25 around a mean difference of -1.00. This interval includes zero and permits effects in either direction. It therefore conveys substantial uncertainty about the contrast between those two dose groups. The registry does not report a p-value for this comparison.

Confidence intervals address sampling uncertainty under the analysis used. They do not resolve uncertainty caused by unreported model specifications, missing-data handling, multiplicity procedures, or the reason for study termination. Nor do they establish whether a difference is clinically important; a threshold for clinical importance is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s design calculation. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. These assumptions describe the illustration only; the trial’s own original sample-size assumptions and justification are not reported in the registry record.

For these continuous-outcome comparisons, the figures mean participants per arm. They are not total sample sizes for the whole trial. The explanation accompanying the planning results distinguishes these from time-to-event calculations, which would be reported as total events; that distinction does not change the meaning of the figures for this continuous endpoint.

In general, the 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the calculation’s assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. These are design-planning concepts, not probabilities that the study result is correct. Smaller target effects require more participants because they are harder to distinguish from random variation.

The rows that use 100%, 75%, and 50% of the observed effect therefore explore progressively smaller target effects. The resulting participant counts rise as the assumed effect becomes smaller. This is not observed power: the figures are prospective planning illustrations derived from the observed estimate, not a measure of the probability that this completed trial detected an effect.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -3.360; pooled standard deviation σ = 3.725.
2. n = 2 × (1.96 + 0.842)² × 3.725² / -3.360² = 19.3, rounded up to 20 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 <- -3.36                      # observed difference in means
sigma <- 3.72451339103513                     # 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(4035668)
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 = 20 (80% power), 26 (90% power)
 75% of observed effect: n per arm = 35 (80% power), 46 (90% power)
 50% of observed effect: n per arm = 78 (80% power), 104 (90% power)
power.t.test: 20.3 
Simulated power at n = 20 per arm: 0.796 (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 reported primary analysis compares any remibrutinib with placebo using MMRM. It reports a mean difference of -2.86, a 95% confidence interval from -4.71 to -1.01, and p = 0.002. The separate dose-group analysis reports a mean difference of -1.00 with a 95% confidence interval from -3.24 to 1.25; a p-value is not reported for that comparison.

The recalculation is a simple unadjusted comparison based on the posted arm summaries. It yields -2.86, a 95% confidence interval from -4.679 to -1.041, and an unadjusted p-value of 0.002 for any remibrutinib versus placebo. These calculations are not identical: the sponsor’s analysis uses the registered repeated-measures model, whereas the recalculation does not reproduce that model. The recalculated standard deviations are also approximate values inferred from the posted standard errors.

The discrepancy flag is true. Accordingly, the sponsor’s own MMRM analysis takes precedence as the trial’s reported result. The recalculation is useful only as a transparent, simplified cross-check of the posted summaries; it should not be presented as a replacement for the registry’s model-based analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 17 outcome measures and 70 analyses, including a primary Week 24 ESSDAI outcome and multiple secondary measures and comparisons. It reports p = 0.002 for the MMRM comparison of any remibrutinib with placebo. The multiplicity strategy, including whether the primary and secondary comparisons were adjusted or arranged in a hierarchy, is not reported in the registry record. Without that information, the p-values for secondary or additional comparisons should be read as unadjusted unless the record explicitly states otherwise.

Multiplicity matters in general because testing many hypotheses creates more opportunities for results that appear notable by chance. Adjustments or prespecified testing strategies can address that issue, but the record does not describe one. The listed number of analyses alone does not reveal which comparisons were confirmatory, which were exploratory, or how the sponsor interpreted them in its protocol.

The primary population is described as randomized participants in the Full Analysis Set with a valid assessment for the outcome. The analysis used an MMRM on post-baseline changes through Week 24. However, the record does not report the number of participants with missing Week 24 values, reasons for missingness, the specific method for handling missing data, or sensitivity analyses testing alternative assumptions. The MMRM description does not by itself establish that missingness had no effect on the result.

Other analysis details are also not reported, including the complete model specification and the original sample-size justification. The registry’s stated analysis and population definition are useful, but these omissions constrain an independent assessment of the analysis choices and their impact. No particular missing-data or multiplicity procedure should be assumed.

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: covid-19 pneumonia (4.2%), pneumonia (4.2%), herpes zoster (4.0%).

The registry reports serious adverse events in 3 of 73 participants overall: 1 among 24 in the twice-daily group, 1 among 25 in the once-daily group, and 1 among 24 in placebo. It reports 44 participants with other adverse events overall: 15 in the twice-daily group, 12 in the once-daily group, and 17 in placebo. No deaths were reported in any group. The safety counts use group sizes of 24, 25, and 24, respectively, and the combined any-remibrutinib safety group includes 49 participants.

These are counts of participants recorded with events, not comparisons adjusted for differences in exposure time or other factors. The registry entries do not provide event-specific timing, duration, severity beyond the serious classification, or an adjusted between-group safety analysis. The listed serious-event terms include COVID-19 pneumonia and pneumonia at 4.2% each, and herpes zoster at 4.0%. Those registry entries should be read as reported terms, not as a complete account of all safety findings.

Safety counts from a study of this size are descriptive and do not establish that an event is caused by a study treatment. The study’s termination reason is not reported in the registry record, so it should not be attributed to safety or any other cause.

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

The primary registry result is a Week 24 model-based estimate of the difference in ESSDAI change between any remibrutinib and placebo. Its negative direction reflects a larger estimated decline in the combined remibrutinib group, and the sponsor-reported 95% confidence interval lies below zero. This describes the posted analysis; it is not by itself a clinical recommendation or a guarantee of an individual outcome.

The result does not establish how much of the observed contrast is clinically important. The registry record does not report a threshold for a meaningful ESSDAI change, nor does the primary total score explain which organ-specific domains account for the estimated change. The placebo group’s mean change was also negative, so interpretation depends on the between-group contrast rather than the remibrutinib group’s change alone.

The combined comparison includes both remibrutinib dose groups. The separate dose-group comparison has an interval spanning zero, and the record does not report a p-value for that contrast. The primary result should therefore not be taken as proof that one dose is better than the other. The study is Phase 2, enrollment was 73, and the registry status is terminated. The reason for termination and the original design rationale are not reported.

Nor does this result alone establish how well the estimate would generalize beyond the participants studied, how it relates to all secondary outcomes, or how missing outcome data might affect interpretation. The MMRM estimate and its interval are the sponsor’s posted primary analysis, while the simplified recalculation is only a cross-check and does not replace it. The most defensible reading is limited to the stated population, endpoint, time point, comparison, and analysis.

18. Why This Trial Matters Statistically

Statistically, this trial illustrates why a model-based primary estimate and a simple recalculation from arm summaries should not be treated as the same analysis. The sponsor used an MMRM across post-baseline visits through Week 24, while the recalculation is a simple unadjusted comparison of summary statistics. Their similar point estimates do not erase the methodological difference or the recorded discrepancy; the sponsor’s own analysis takes precedence.

The endpoint also highlights the distinction between within-group change and a randomized comparison. All three primary arm estimates are negative, but the primary question concerns the difference between remibrutinib and placebo. A change in the treatment group alone cannot answer that comparative question. The model-based contrast places both groups in the same analysis and provides an interval for the estimated difference.

The study’s adaptive Phase 2 description makes access to design details especially relevant, yet the registry does not report specific adaptation rules or the original sample-size justification. The planning illustrations use the observed effects and stated assumptions, so they are not substitutes for the original design rationale. Similarly, a broad set of outcomes and analyses makes multiplicity and prespecification important; the strategy for addressing these issues is not reported.

Finally, the registry’s primary analysis population requires a valid assessment, while missing-data handling is not described. Reading the result statistically therefore involves more than checking the estimate or p-value: the endpoint definition, analysis population, model, precision, reporting gaps, and secondary-analysis context all shape what can responsibly be concluded.

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. The study enrolled 73 participants, and the primary endpoint groups each contained 24 participants for the single-dose comparisons and 24 for placebo. The sample was therefore limited in size, and the confidence interval should be considered alongside the point estimate rather than treating the estimate as exact. The reason for the recorded terminated status is not reported in the registry record.

The primary analysis is model-based, but the registry summary does not report the full MMRM specification, including covariance structure and other modeling details. The Full Analysis Set description also requires a valid assessment for the outcome. The number and reasons for missing assessments, the handling of missing data, and sensitivity analyses are not reported. These gaps prevent a full assessment of how the model and available outcome data affect the result.

The record lists 70 analyses and multiple outcomes, but does not report a multiplicity strategy or identify the status of every analysis as confirmatory or exploratory. The original sample-size target and its justification are also not reported. Planning illustrations based on observed effects cannot fill that gap.

Finally, the sponsor’s reported MMRM result differs modestly from the simple unadjusted recalculation, and the discrepancy flag is true. The sponsor analysis takes precedence, but the recalculation underscores that summary-statistic methods do not reproduce the registered model. The registry entries do not provide enough detail to resolve the underlying difference beyond that methodological distinction.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 2 Study to Evaluate the Safety and Efficacy of LOU064 in Patients With Moderate to Severe Sjögren's Syndrome — NCT04035668.
• Registry record last updated 2023-01-30; status last verified 2023-01.
• Results first posted 2022-12-20.
• 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

NCT04035668 is a randomized, triple-masked, parallel-group, placebo-controlled Phase 2 study of remibrutinib in moderate to severe Sjögren's syndrome. The registry records 73 participants and a terminated status. The primary outcome is change in ESSDAI total score at Week 24, analyzed with MMRM in the Full Analysis Set among participants with a valid outcome assessment.

The sponsor reports an any-remibrutinib versus placebo mean difference of -2.86, with a 95% confidence interval from -4.71 to -1.01 and p = 0.002. A simple recalculation is close but not identical; because the discrepancy flag is true, the sponsor’s analysis takes precedence. The registry does not report the original sample-size rationale, missing-data details, multiplicity strategy, or reason for termination. Secondary outcomes cover clinical, patient-reported, safety, and pharmacokinetic measures, while the posted safety summary records 3 serious adverse events and no deaths.