Study of Safety and Efficacy of Multiple Doses of CFZ533 in Two Distinct Populations of Patients With Sjogren's Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Safety and Efficacy of Multiple Doses of CFZ533 in Two Distinct Populations of Patients With Sjogren's Syndrome (NCT03905525), a randomized phase 2 study. The primary outcome is Cohort 1: Change in EULAR Sjögren Syndrome Disease Activity Index (ESSDAI) Score From Baseline at 24 Weeks as Compared to Placebo.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, quadruple-masked, parallel-group trial described as a 48-week, 6-arm, placebo-controlled study of multiple subcutaneous CFZ533 doses in two distinct populations of patients with Sjögren’s syndrome. The registry lists an enrollment of 273 and a completed status. The study was sponsored by Novartis Pharmaceuticals. It began on 2019-10-01, and primary completion was recorded as 2022-09-28.

The primary endpoint is a Week 24 outcome in Cohort 1. That cohort included three active-dose groups and a placebo group during Period 1. Participants in the placebo group began iscalimab in Period 2, while the active-dose groups continued their assigned dosing schedules. Cohort 2 also had an active-dose group and a placebo group in Period 1, with active treatment beginning in Period 2 for the placebo group. The specific criteria defining the two cohorts are not reported in the registry record.

The registry describes weekly loading doses followed by bi-weekly subcutaneous administrations. For Cohort 1, the active regimens used 600 mg loading doses followed by 150 mg, 300 mg, or 600 mg bi-weekly. The placebo group received placebo through Week 22 before the Period 2 regimen. The study’s brief description says it evaluated safety, efficacy, pharmacokinetics, and pharmacodynamics. The original sample-size justification, the trial’s prespecified statistical plan, and details of any interim analyses 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.

Only the first 6 of 8 groups are shown.

Period 1 (up to Week 24): Cohorts 1&2

Reasons for not completing this period:

Period 2 (up to Week 48): Cohorts 1&2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set. Only participants in cohort 1 with a value at both Baseline and post-baseline visit included.

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: Demographics and Baseline Characteristics were assessed in Period 1.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Cohort 1: Change in EULAR Sjögren Syndrome Disease Activity Index (ESSDAI) Score From Baseline at 24 Weeks as Compared to Placebo, measured over Baseline, Week 24.

The primary outcome is change from baseline in the EULAR Sjögren Syndrome Disease Activity Index (ESSDAI) score at Week 24. ESSDAI is described in the registry as a validated disease outcome measure with 12 organ-specific domains. Each domain scores features of disease activity across severity levels, and the domain scores are combined using weights to form a total score. The total can range from 0-123. The registry describes low activity as ESSDAI < 5, moderate activity as 5-13, and high activity as ESSDAI >= 14.

ESSDAI is used to represent disease activity across organ systems rather than a single symptom or organ. A change from baseline summarizes how the score differs at the follow-up assessment from each participant’s baseline score. The posted group estimates are least-squares means, with standard errors reported as their dispersion measure. Negative changes indicate lower scores relative to baseline, but the registry record does not specify a threshold for a clinically important change. A group-average change also does not describe the range of individual participant experiences.

The endpoint comparison is placebo versus each Cohort 1 dose at Week 24. It is not a comparison of every treatment group across the full 48-week period. The primary population includes participants with a baseline and post-baseline value, according to the registry’s description.

7. Results Posted in the Registry

• Cohort 1/Arm C: CFZ533 150 mg: mean -7.00 versus -4.00 on control; difference -3.00 (95% CI -4.98 to -1.02), standardized effect d = -0.65; z-test p = 0.003.
• Cohort 1/Arm B: CFZ533 300 mg: mean -5.40 versus -4.00 on control; difference -1.40 (95% CI -3.40 to 0.60), standardized effect d = -0.30; z-test p = 0.169.
• Cohort 1/Arm A: CFZ533 600 mg: mean -6.90 versus -4.00 on control; difference -2.90 (95% CI -4.92 to -0.88), standardized effect d = -0.63; z-test p = 0.005.

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.

Cohort 1: Change From Baseline in ESSPRI 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 errors.
• Result:
  • Cohort 1/Arm C: CFZ533 150 mg: mean -1.80 versus -1.30 on control; difference -0.50 (95% CI -1.35 to 0.35), standardized effect d = -0.26; z-test p = 0.246.
  • Cohort 1/Arm B: CFZ533 300 mg: mean -1.60 versus -1.30 on control; difference -0.30 (95% CI -1.16 to 0.56), standardized effect d = -0.15; z-test p = 0.494.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 1/Arm C: CFZ533 150 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 Cohort 1/Arm B: CFZ533 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Cohort 1: Change From Baseline in Score of Functional Assessment of Chronic Illness Therapy - Fatigue (FACIT-F) Questionnaire 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 errors.
• Result:
  • Cohort 1/Arm C: CFZ533 150 mg: mean 8.60 versus 7.00 on control; difference 1.60 (95% CI -2.46 to 5.66), standardized effect d = 0.17; z-test p = 0.440.
  • Cohort 1/Arm B: CFZ533 300 mg: mean 8.00 versus 7.00 on control; difference 1.00 (95% CI -3.09 to 5.09), standardized effect d = 0.11; z-test p = 0.632.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 1/Arm C: CFZ533 150 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 Cohort 1/Arm B: CFZ533 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Cohort 1: Change From Baseline in Physician Global Assessment (PhGA) 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 errors.
• Result:
  • Cohort 1/Arm C: CFZ533 150 mg: mean -31.60 versus -23.90 on control; difference -7.70 (95% CI -15.70 to 0.30), standardized effect d = -0.43; z-test p = 0.059.
  • Cohort 1/Arm A: CFZ533 600 mg: mean -27.00 versus -23.90 on control; difference -3.10 (95% CI -11.15 to 4.95), standardized effect d = -0.17; z-test p = 0.451.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 1/Arm C: CFZ533 150 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 Cohort 1/Arm A: CFZ533 600 mg and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover participant-reported symptoms and fatigue, physician assessment, disease activity, eye-related symptom bother, and adverse events. The reported Cohort 1 continuous outcomes include ESSPRI, FACIT-F, and PhGA; Cohort 2 outcomes include FACIT-F, PhGA, ESSDAI, and an IDEEL response measure. The registry lists 21 outcome measures and 19 posted secondary outcomes. The secondary results are not a single unified measure, and their scales and meanings differ.

Across the posted Cohort 1 secondary comparisons with recalculated contrasts, the confidence intervals include zero for ESSPRI and FACIT-F. The PhGA 150 mg comparison has an interval that includes zero but is close to it, while the 600 mg comparison has an interval that includes zero. The sponsor’s reported mixed-model intervals and p-values are also posted for these comparisons. These are descriptive observations about the recorded estimates, not a basis for selecting a preferred result among multiple outcomes.

The secondary outcomes provide additional context around the primary ESSDAI comparison, but they do not independently confirm or overturn it. They assess different aspects of the condition, involve different groups or analysis populations, and may have different amounts of missing information. The primary result remains the prespecified primary outcome as named in the registry; the secondary measures broaden the set of questions but do not have the same inferential status.

Unadjusted secondary results carry less weight because many outcomes and comparisons create more opportunities for apparently notable findings by chance. General explanation: multiplicity adjustment or a prespecified hierarchy can help control the interpretation of repeated testing. Whether such a strategy was planned or used is not reported in the registry record. Secondary estimates are therefore best read as supportive and exploratory context unless the full analysis plan establishes otherwise.

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

• Cohort 1: Change From Baseline in ESSPRI at Week 24
• Cohort 1: Change From Baseline in Score of Functional Assessment of Chronic Illness Therapy - Fatigue (FACIT-F) Questionnaire at Week 24
• Cohort 1: Change From Baseline in Physician Global Assessment (PhGA) at Week 24
• Cohort 2: Change From Baseline in Score of Functional Assessment of Chronic Illness Therapy - Fatigue (FACIT-F) Questionnaire at Week 24
• Cohort 2: Change From Baseline in Physician Global Assessment (PhGA) at Week 24
• Cohort 2: Change From Baseline in ESSDAI at Week 24
• Cohort 2: Proportion of Subjects With at Least 12 Points Improvement Measured by Score of Impact of Dry Eye on Everyday Life (IDEEL) Questionnaire Symptom Bother Module at Week 24.
• Cohort 1: Incidence of Adverse Events (AEs), Serious Adverse Events (SAEs) up to Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

These results involve group means, adjusted model estimates, uncertainty intervals, and hypothesis tests. The distinctions matter: a within-group change is not the same quantity as a between-group difference, and a numerical difference is not by itself evidence of clinical importance.

What does a least-squares mean represent?

The registry reports least-squares means for change from baseline. In general, a least-squares mean is an estimate from a statistical model rather than a simple arithmetic average of the observed values. Models can account for features specified in their analysis, but the registry record does not provide the full model specification. The posted primary group estimates are -4.0 for placebo, -7.0 for 150 mg, -5.4 for 300 mg, and -6.9 for 600 mg. Each is a change from baseline within a group. The comparison of interest is the model-based difference between a dose group and placebo.

How should the treatment contrast be read?

The reported contrast is labeled as the least-squares mean difference CFZ533 minus placebo. Thus, the reported -3.0 for 150 mg is the sponsor’s estimated group contrast, not the within-group change in that arm. Negative values indicate a more negative estimated change in the CFZ533 group relative to placebo on this outcome scale. That numerical direction should not be converted into a claim about clinical benefit without considering the measure’s interpretation, uncertainty, and clinical importance. The record does not state a threshold for a clinically important difference.

What does the standard error describe?

The registry lists standard error as the dispersion measure for the least-squares means. General explanation: a standard error describes the uncertainty in an estimated mean. It is not the spread of individual participant scores. A confidence interval uses uncertainty around an estimate to describe a range of values compatible with the analysis, under its statistical assumptions. The sponsor reports 95% confidence intervals for the primary contrasts; the arms’ posted standard errors are 0.73, 0.7, 0.71, and 0.73 in the order placebo, 150 mg, 300 mg, and 600 mg.

What is the role of a p-value?

General explanation: a p-value describes how compatible the observed data are with a specified null hypothesis under a statistical model. It does not give the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The sponsor reports p-values of 0.003, 0.158, and 0.004 for the primary comparisons. These values should be considered together with the estimated contrasts and confidence intervals. The record does not report whether the primary comparisons were adjusted for testing multiple doses.

What was recalculated?

The posted recalculations are simple, unadjusted comparisons derived from the group means and standard errors. They approximate pooled variability and standardize the mean difference for an effect-size summary. General explanation: standardizing a difference can help describe its size relative to variability, but it does not replace the trial’s prespecified model. The recalculated uncertainty and p-values can differ from the sponsor’s mixed-model results because they do not reproduce the sponsor’s model. The calculations also use an approximate standard deviation derived from reported standard errors. Since the registry record flags a discrepancy, the sponsor analysis takes precedence.

The distinction between the populations also matters. The primary endpoint description specifies the Full Analysis Set and includes only Cohort 1 participants with a value at baseline and a post-baseline visit. The record does not describe how missing observations were handled in the sponsor’s model, whether other analysis populations were used for the primary endpoint, or whether sensitivity analyses were conducted. These details limit what can be inferred from the posted summary statistics alone.

Finally, statistical significance and precision are related but not interchangeable. A p-value is a test summary, while the interval shows a range of estimated contrasts compatible with the analysis. Neither one establishes clinical importance. The endpoint’s scale, population, model, missing-data handling, and multiplicity strategy all inform how the findings should be read. Where those elements are absent from the registry record, interpretation should remain limited to the reported estimates and their uncertainty.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals give the uncertainty around the estimated Week 24 differences from placebo. For 150 mg, the reported difference is -3.0 and its interval is -4.9 to -1.1. For 300 mg, the reported difference is -1.4 and its interval is -3.3 to 0.5. For 600 mg, the reported difference is -2.9 and its interval is -4.9 to -1.0. The intervals for 150 mg and 600 mg do not include zero; the 300 mg interval does.

General explanation: a confidence interval is a range generated by a statistical procedure that reflects uncertainty in an estimate under the model’s assumptions. It is not a range containing a known proportion of individual participant outcomes, and it does not show the probability that the true effect lies within that particular interval. Wider intervals indicate less precision than narrower intervals, all else being equal.

The registry also contains recalculated intervals based on posted means and standard errors. For 150 mg, the recalculated interval is -4.982 to -1.018; for 300 mg, it is -3.396 to 0.596; and for 600 mg, it is -4.923 to -0.877. These approximate unadjusted intervals are not identical to the sponsor-reported intervals. The discrepancy is a reason to use the sponsor’s mixed-model results as the primary inferential results.

Intervals that include zero are compatible with a range of contrasts on both sides of no difference under the analysis. Intervals excluding zero do not, by themselves, convey whether the estimated contrast is important to patients or robust to analysis choices. The registry record does not report a clinical-importance threshold or the full model details needed to independently assess all sources of uncertainty.

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 are planning calculations based on the observed effect, not the trial’s original design justification. For these continuous outcomes, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each calculation targets the stated fraction of the observed effect. The trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a future comparison to have 80% power under those assumptions, if the effect to detect is the specified fraction of the observed effect. The 90% power column gives the corresponding illustration for 90% power. General explanation: power is the probability of detecting an effect under a specified model and assumptions when that effect is present. These planning values are not observed power for the completed trial.

Rows that use 100% of the observed effect use the observed contrast as the planning target; rows using 75% or 50% plan for smaller effects than the observed one. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under the same assumptions. The illustrations are not guarantees: actual precision and power can differ if the future study’s population, variability, allocation, analysis, or effect differs from the planning assumptions. They should be read as conditional planning examples, not as a reconstruction of the trial’s original enrollment rationale.

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 = -3.000; pooled standard deviation σ = 4.605.
2. n = 2 × (1.96 + 0.842)² × 4.605² / -3.000² = 37.0, rounded up to 37 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                      # observed difference in means
sigma <- 4.6050643083404                     # 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(3905525)
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 = 37 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 89 (90% power)
 50% of observed effect: n per arm = 148 (80% power), 199 (90% power)
power.t.test: 38 
Simulated power at n = 37 per arm: 0.790 (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 registry’s sponsor-reported primary analysis used mixed models and reports least-squares mean differences between CFZ533 and placebo. Its estimates are -3.0 for 150 mg, -1.4 for 300 mg, and -2.9 for 600 mg, with respective 95% confidence intervals of -4.9 to -1.1, -3.3 to 0.5, and -4.9 to -1.0. The sponsor-reported p-values are 0.003, 0.158, and 0.004.

Separate recalculations use the posted group means and standard errors to form simple unadjusted comparisons. Their estimates are -3.0, -1.4, and -2.9, but their confidence limits and p-values are not identical to the sponsor’s mixed-model results. The recalculated p-values are 0.003, 0.169, and 0.005. These calculations do not reproduce the sponsor’s model and use approximate variability derived from the posted summary statistics.

The registry record flags a discrepancy between the sponsor analysis and recalculations. The sponsor’s own analysis therefore takes precedence for interpreting the trial’s reported inferential results. The recalculations are useful as a transparent check on the broad scale and direction of the contrasts, but should not be treated as equivalent to the sponsor’s analysis or as evidence that the sponsor’s model has been replicated.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 21 outcome measures, 17 analyses, and 19 posted secondary outcomes. The primary outcome includes comparisons of three CFZ533 doses with placebo. The record reports sponsor p-values and confidence intervals for the primary contrasts and for posted secondary comparisons, but whether the primary dose comparisons were adjusted for multiplicity is not reported in the registry record. The same is true of the adjustment strategy for the secondary analyses and whether a hierarchy or other testing sequence was prespecified.

General explanation: testing multiple outcomes or treatment contrasts increases the chance of obtaining at least one apparently unusual result under a setting where no true effects exist. A prespecified multiplicity strategy can address this issue, but the choice of approach depends on the trial’s objectives and analysis plan. Without the plan, unadjusted p-values should not be read as if they necessarily control the overall error rate across the collection of tests.

The primary analysis population is described as the Full Analysis Set, with only Cohort 1 participants having both baseline and post-baseline values included. The registry does not report the detailed handling of missing Week 24 measurements, the model’s assumptions for incomplete data, or sensitivity analyses assessing those assumptions. The number and characteristics of participants with missing endpoint values are not reported in the registry record.

These omissions matter because estimates can depend on who contributes data and how missing outcomes are handled. The posted group counts for the primary analysis do not explain why the analyzed numbers differ across arms or how participants without complete measurements were treated. The trial’s original sample-size rationale, detailed prespecified statistical analysis plan, and any interim-analysis procedures are also not reported. Consequently, the registry supports a description of the posted analyses, but not a full audit of the planned inferential framework.

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: cholecystitis (2.4%), tuberculosis (2.4%), osteoarthritis (2.4%), nephrolithiasis (2.4%), enteritis (2.4%).

The safety record lists serious adverse events and other adverse events by treatment group, along with the number at risk for each category and deaths. For example, serious adverse events were reported for 1 of 43 participants at risk in Cohort 1 placebo, 6 of 44 in the 150 mg group, 6 of 42 in the 300 mg group, and 6 of 44 in the 600 mg group. The Period 2 Cohort 1 group receiving 600 mg had 4 of 41 participants with a serious adverse event. These counts describe the registry’s recorded groups and periods.

The record also lists one death in Cohort 1 Arm B and one in Cohort 2 Arm E; deaths are listed as zero in the other groups. The cause of death, relationship to treatment, timing, and circumstances are not reported in the registry record. The most frequently listed serious-event terms each have a reported frequency of 2.4%: cholecystitis, tuberculosis, osteoarthritis, nephrolithiasis, enteritis, and haematochezia.

Counts at risk and affected are not a substitute for event-level details or adjusted comparisons. Treatment exposure differs across the trial periods, and the Period 2 groups should not be read as direct randomized comparisons with the Period 1 placebo groups. The registry record does not provide enough detail to determine causality or compare risks formally.

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

The primary results describe Week 24 ESSDAI changes in Cohort 1 and the sponsor’s estimated differences between each active dose and placebo. The sponsor reports negative contrasts for all three doses; the 150 mg and 600 mg confidence intervals exclude zero, while the 300 mg interval includes zero. This is a statistical description of the posted analysis, not a conclusion about clinical benefit or lack of benefit.

A confidence interval and p-value cannot answer whether a difference is important to participants. The registry record does not report a threshold for clinical importance, and group averages do not show how many individuals experienced improvement, worsening, or no change. The estimates also concern a Week 24 endpoint in Cohort 1, not the full range of outcomes or the entire study period.

The trial had two distinct cohorts, but the cohort-defining criteria are not reported in the registry record. The primary analysis population includes Cohort 1 participants with baseline and post-baseline values. Missing-data handling, adjustment for multiple comparisons, and the full model specification are also not reported. Those gaps limit independent assessment of how robust the estimates are to analysis choices.

The safety counts are descriptive and include treatment-period differences. The record does not establish that an adverse event was caused by study treatment, and it does not provide enough detail to interpret the listed deaths. Likewise, the planning illustrations based on observed effects are not evidence of the trial’s achieved power. The most defensible reading is therefore narrow: the registry reports particular group changes, model-based contrasts, uncertainty intervals, p-values, and safety counts for the populations and time points specified.

18. Why This Trial Matters Statistically

This trial illustrates why clinical-trial interpretation requires separating within-group change from the comparison between randomized groups. The posted ESSDAI means show changes from baseline, while the primary treatment contrasts estimate differences between each CFZ533 dose and placebo. Conflating those quantities can make a group’s change appear to answer a comparative question that it does not answer.

It also demonstrates why sponsor-reported model results and simple recalculations may not match exactly. The recalculations provide a check using posted summary statistics, but do not reproduce a mixed model. When the registry flags a discrepancy, the sponsor’s analysis takes precedence. This distinction is especially important when confidence limits or p-values are close to conventional thresholds.

The trial also raises practical questions about multiplicity, missing outcomes, and population definitions. Several doses and outcome measures are reported, but adjustment procedures and detailed missing-data methods are not reported in the registry record. These choices affect how strongly individual findings can be interpreted. The distinction between the Cohort 1 primary outcome and the broader set of secondary outcomes should remain visible when evaluating the evidence.

Finally, planning calculations based on observed effects should not be mistaken for the trial’s original design rationale or for observed power. They illustrate how required enrollment changes with the assumed effect under stated assumptions. Together, these issues make the record useful for understanding the reported estimates while also showing why statistical conclusions depend on more than a point estimate or a p-value.

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.

The registry summary does not report the criteria defining Cohort 1 and Cohort 2, limiting assessment of how the two populations differ or to whom each set of results applies. The primary endpoint analysis is restricted to Cohort 1 participants with baseline and post-baseline ESSDAI values, but the record does not give detailed reasons for missing values or describe the missing-data method used by the sponsor.

The sponsor reports mixed-model analyses, but the full model specification is not reported. The registry also does not state whether primary dose comparisons or secondary tests were adjusted for multiplicity, or whether a testing hierarchy was prespecified. These details are needed to assess the inferential interpretation of multiple comparisons. The original sample-size justification and any interim-analysis plans are not reported.

The posted recalculations rely on approximate variability derived from standard errors and are unadjusted. They are not substitutes for the sponsor’s analysis, particularly because the registry indicates a discrepancy. The planning illustrations are based on observed effects and stated assumptions, rather than the trial’s original design assumptions.

The primary efficacy comparison is at Week 24, although the trial is described as lasting 48 weeks. The posted primary results do not establish the pattern of outcomes over the full trial period. The registry summary also does not report a clinically important ESSDAI difference, individual response distributions, or enough event detail to attribute adverse events to treatment. These limitations constrain both clinical interpretation and independent reproduction of the analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Safety and Efficacy of Multiple Doses of CFZ533 in Two Distinct Populations of Patients With Sjogren's Syndrome — NCT03905525.
• Registry record last updated 2026-05-18; status last verified 2026-04.
• Results first posted 2026-05-18.
• 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

NCT03905525 is a completed Phase 2 randomized, quadruple-masked, parallel-group study of subcutaneous CFZ533 in patients with Sjögren’s syndrome. The trial record describes two distinct cohorts, placebo-controlled treatment periods, and a 48-week study. The primary outcome is Cohort 1 change from baseline in ESSDAI at Week 24.

The sponsor’s mixed-model analysis reports differences from placebo of -3.0 for 150 mg, -1.4 for 300 mg, and -2.9 for 600 mg. The reported 95% confidence intervals exclude zero for the 150 mg and 600 mg comparisons and include zero for the 300 mg comparison. The record flags a discrepancy with approximate unadjusted recalculations, so the sponsor’s analysis takes precedence.

Secondary outcomes and safety counts add context, but multiplicity procedures, detailed missing-data methods, and the original sample-size justification are not reported in the registry record. The posted estimates should be interpreted within those limits.