Study to Assess Safety and Efficacy of Filgotinib, Lanraplenib and Tirabrutinib in Adults With Active Sjogren's Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess Safety and Efficacy of Filgotinib, Lanraplenib and Tirabrutinib in Adults With Active Sjogren's Syndrome (NCT03100942), a randomized phase 2 study. The primary outcome is Percentage of Participants Fulfilling Protocol-Specified Response Criteria at Week 12, as Compared to Baseline.

2. Clinical Question

The response definition combined participant-reported symptoms with an hsCRP condition. Participants had to improve by at least 20% in at least 3 of 5 Sjogren's syndrome-related visual analogue score measures: global disease assessment, pain, oral dryness, ocular dryness, and fatigue. None of those measures could increase by more than 30 mm from baseline. The response definition also required either the specified hsCRP improvement for participants whose baseline hsCRP was at least 1.5 times the upper limit of normal, or no increase to that threshold for those whose baseline hsCRP was lower.

This is a composite definition: meeting the endpoint depends on satisfying its symptom and hsCRP requirements together. It therefore addresses a particular protocol-defined pattern of change, rather than a single symptom or a general statement about all aspects of the disease.

3. Trial Design

The registry record describes a completed, randomized, double-blind, parallel-group, phase 2 study sponsored by Gilead Sciences. It enrolled adults with active Sjogren's syndrome. The recorded study start was 2017-05-01, and primary completion was 2019-01-10. The listed enrollment was 152.

Participants were assigned to lanraplenib, filgotinib, tirabrutinib, or placebo, with matching placebos used to maintain blinding across the study-drug regimens. The active treatment descriptions list treatment durations of up to 49.4 weeks for lanraplenib, 50.4 weeks for filgotinib, and 50.3 weeks for tirabrutinib. The placebo description specifies placebo through Week 24 and then blinded rerandomization after the Week 24 assessments to receive an active study drug through Week 48.

The primary outcome was the percentage meeting protocol-defined response criteria at Week 12, compared with baseline. That timing places the primary assessment during the placebo-controlled period. The registry also reports secondary changes from baseline in ESSDAI and ESSPRI at Week 12 and Week 24. ESSDAI is the EULAR Sjogren's Syndrome Disease Activity Index; ESSPRI is the EULAR Sjogren's Syndrome Patient Reported Index.

The registry record does not report the original sample-size justification, detailed randomization procedures, or the complete statistical analysis plan. It also does not report the intended handling of every post-randomization event or the full details of the later active-treatment assignments. Those details should not be inferred from the posted outcome summaries.

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: 348 participants were screened.

Only the first 6 of 7 groups are shown.

Randomized Treatment Period

Reasons for not completing this period:

Placebo Arm Re-Randomized

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set included all randomized participants who received at least one dose of study drug. Included participants with available data.

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: The Safety Analysis Set included participants who received at least one dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Fulfilling Protocol-Specified Response Criteria at Week 12, as Compared to Baseline, measured over Week 12.

The primary endpoint is the percentage of participants who fulfilled the study's response definition at Week 12, relative to baseline. It combines change in five participant-reported visual analogue score measures with a rule for hsCRP. To qualify, a participant needed at least 20% improvement in at least 3 of the 5 symptom measures, without an increase greater than 30 mm from baseline in any of them. The hsCRP requirement depended on the baseline hsCRP level: participants starting at or above 1.5 times the upper limit of normal needed the specified improvement, while those starting below that level could not increase to the threshold.

A composite endpoint can represent more than one aspect of a condition within a single outcome. It also makes the meaning of response specific to the criteria: a participant must satisfy the combined rules, rather than show improvement on only one component. The endpoint is expressed as a percentage because the outcome is whether each participant met the response definition.

The registry identifies the Full Analysis Set as randomized participants who received at least one dose of study drug, with participants included when data were available. The endpoint's results therefore describe the recorded responses in that analysis population, not necessarily every randomized participant. How unavailable Week 12 data were handled beyond this inclusion description is not reported in the registry record.

7. Results Posted in the Registry

• Lanraplenib: 42.9% (15/35) versus 26.5% (9/34) on control; risk difference 16.4 percentage points (95% CI -5.7 to 38.5), risk ratio 1.62 (0.82–3.19); unadjusted two-proportion z-test p = 0.153.
• Filgotinib: 43.2% (16/37) versus 26.5% (9/34) on control; risk difference 16.8 percentage points (95% CI -5.0 to 38.6), risk ratio 1.63 (0.84–3.20); unadjusted two-proportion z-test p = 0.139.
• Tirabrutinib: 35.1% (13/37) versus 26.5% (9/34) on control; risk difference 8.7 percentage points (95% CI -12.7 to 30.0), risk ratio 1.33 (0.65–2.70); unadjusted two-proportion z-test p = 0.430.

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.

Change From Baseline in European League Against Rheumatism (EULAR) Sjogren's Syndrome Disease Activity Index (ESSDAI) at Week 12

• 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:
  • Lanraplenib: mean -2.50 versus -3.90 on control; difference 1.40 (95% CI -0.71 to 3.51), standardized effect d = 0.30; z-test p = 0.193.
  • Filgotinib: mean -4.70 versus -3.90 on control; difference -0.80 (95% CI -2.85 to 1.25), standardized effect d = -0.18; z-test p = 0.445.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lanraplenib 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 Filgotinib and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in EULAR Sjogren's Syndrome Patient Reported Index (ESSPRI) at Week 12

• 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:
  • Lanraplenib: mean -1.00 versus -1.00 on control; difference 0.00 (95% CI -0.94 to 0.94), standardized effect d = 0.00; z-test p = 1.000.
  • Filgotinib: mean -1.40 versus -1.00 on control; difference -0.40 (95% CI -1.33 to 0.53), standardized effect d = -0.20; z-test p = 0.399.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lanraplenib 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 Filgotinib and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in ESSDAI 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:
  • Lanraplenib: mean -4.30 versus -4.20 on control; difference -0.10 (95% CI -2.30 to 2.10), standardized effect d = -0.02; z-test p = 0.929.
  • Filgotinib: mean -5.40 versus -4.20 on control; difference -1.20 (95% CI -3.32 to 0.92), standardized effect d = -0.26; z-test p = 0.267.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lanraplenib 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 Filgotinib and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover two related but distinct domains: ESSDAI, a disease-activity index, and ESSPRI, a patient-reported index. The registry reports changes from baseline at Week 12 and Week 24. Across these endpoints, the posted estimates do not form a consistent pattern of clear separation from placebo. Some group estimates show greater changes from baseline than placebo, while other estimates are close to the placebo estimate; the reported comparison intervals include zero for the sponsor analyses listed.

These outcomes provide additional context alongside the primary Week 12 response endpoint, but they are not interchangeable with it. The primary outcome requires meeting a composite response rule based on symptom measures and hsCRP. ESSDAI and ESSPRI instead summarize changes on their respective scales. Variation across these measures is possible because they assess different aspects of the condition and use different definitions.

Secondary findings should carry less weight than the primary result when they are interpreted without adjustment for multiple comparisons. Examining several outcomes and time points increases the opportunity for apparently notable results to arise by chance. The registry record does not report a multiplicity adjustment strategy for these outcomes, so the posted secondary p-values should be treated as exploratory rather than as independent confirmatory evidence.

The registry reports secondary results for lanraplenib and filgotinib comparisons in the listed analyses, while tirabrutinib is not included in the posted secondary comparison entries shown for these outcomes. The reason for that pattern is not reported in the registry record. No stronger conclusion about comparative benefit should be drawn from the secondary results alone.

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

• Change From Baseline in European League Against Rheumatism (EULAR) Sjogren's Syndrome Disease Activity Index (ESSDAI) at Week 12
• Change From Baseline in EULAR Sjogren's Syndrome Patient Reported Index (ESSPRI) at Week 12
• Change From Baseline in ESSDAI at Week 24
• Change From Baseline in ESSPRI at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports the primary outcome as a percentage of participants fulfilling a binary response definition. For each participant, the endpoint is whether the specified criteria were met at Week 12. Group percentages describe the share meeting that definition; they do not describe the average magnitude of symptom change among all participants.

How should the response-rate comparison be read?

The sponsor reports differences in response rates using the Cochran-Mantel-Haenszel method. This method compares categorical outcomes across groups and can account for stratification factors when those are part of the analysis. The specific stratification factors and detailed implementation are not reported in the registry record, so they should not be inferred. The reported estimate is a difference in response rates, with a confidence interval expressing uncertainty around that estimate.

A difference of zero would correspond to equal response rates between the compared groups. The confidence intervals for all three reported comparisons include zero. This is consistent with the reported p-values not indicating a clear difference under the analyses as posted. A p-value does not measure the size or importance of an effect, and it is not the probability that a treatment works or that the null hypothesis is true.

What do the recalculated comparisons add?

The simple recalculations use the posted response counts and denominators to estimate unadjusted risk differences and their intervals. An unadjusted estimate compares the observed group summaries without incorporating any adjustment that may be used in the sponsor's analysis. Such recalculations can help readers understand the basic contrast, but they can differ from an adjusted analysis because the methods and inputs differ. The reported analyses, rather than the recalculations, are the registry's own comparative results.

The recalculated risk-difference estimates are 0.164 for lanraplenib, 0.168 for filgotinib, and 0.087 for tirabrutinib, each compared with placebo. Their intervals are -0.057 to 0.385, -0.050 to 0.386, and -0.127 to 0.300, respectively. All include zero. These are unadjusted recalculations, not a replacement for the sponsor's analysis.

What do the continuous-outcome analyses represent?

For the secondary ESSDAI and ESSPRI outcomes, the registry reports least-squares means and standard errors, and lists mixed model for repeated measures (MMRM) for the sponsor's comparisons. In general, MMRM is a method for analysing repeated measurements while representing within-participant correlation over time. It can use observations at multiple visits and estimate group differences while accounting for the repeated-measures structure. The specific model terms, covariance structure, and missing-data assumptions are not reported in the registry record.

A least-squares mean is a model-based group estimate, not necessarily the simple arithmetic average of observed participant values. A standard error describes the estimated uncertainty of that mean. The sponsor reports 95% confidence intervals and p-values for the listed comparisons. These results should be understood as model-based analyses rather than as simple comparisons of the displayed group means.

The separate recalculations for continuous outcomes are unadjusted mean differences based on posted summary statistics. The pooled standard deviations used for those recalculations are approximate because the posted summaries give standard errors rather than participant-level variability. This approximation limits how closely the recalculated interval or planning illustration can reproduce an analysis of the original data.

Why does over-dispersion matter in general?

In general, over-dispersion occurs when observed variation is greater than a model assumes. For binary outcomes, a model that understates variability can produce confidence intervals that are too narrow and tests that appear more decisive than the data warrant. Appropriate modelling of the outcome and design is important; the registry record does not identify an over-dispersion issue for these results.

Randomization and double blinding are design features intended to reduce systematic differences in treatment assignment and expectations. They do not eliminate sampling uncertainty, missing data, or limitations in outcome measurement. The registry record does not provide enough detail to evaluate every implementation aspect of these methods.

11. Confidence Intervals and Precision

The 95% confidence intervals around the primary sponsor-reported differences are wide and include zero for each active-treatment comparison. For lanraplenib, the reported difference was 15.6, with an interval from -6.3 to 37.6. For filgotinib, it was 16.6, with an interval from -5.1 to 38.3. For tirabrutinib, it was 8.1, with an interval from -13.2 to 29.4. Each interval allows for a range of plausible differences, including no difference and values in either direction.

A confidence interval is a way to express sampling uncertainty around an estimate. In general, a wider interval indicates less precision, while a narrower interval indicates more precision, given the analysis and its assumptions. An interval that includes zero does not prove that the groups are the same; it indicates that the data do not precisely distinguish the estimated difference from no difference at the stated confidence level.

The observed percentages and comparative estimates should therefore be read together with their intervals, not as exact treatment effects. The recalculated unadjusted intervals also include zero, but they use a simpler method than the sponsor's reported comparison. The registry's reported analysis is the more relevant result for describing the trial's own comparison.

Precision is also affected by the endpoint's definition and the available observations. The Full Analysis Set description includes participants with available data, but the detailed handling of missing endpoint observations is not reported in the registry record. That uncertainty in the analysis details should be kept separate from the sampling uncertainty represented by the confidence intervals.

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 observed effects, not the trial's original design assumptions. The registry record does not report the original sample-size justification. For the binary primary endpoint and the listed continuous outcomes, the figures are participants per arm; time-to-event planning tables, if present, would instead report total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the approximate participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column makes the same kind of planning statement with a higher target chance of detection. These are design illustrations, not guarantees about any future trial.

Rows that plan for 75% or 50% of the observed effect consider smaller effects than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm in these illustrations. The estimates inherit uncertainty from the observed effect, and the continuous-outcome calculations use approximate variability reconstructed from the posted summaries.

This is not observed power. Observed power is not a useful substitute for reading the effect estimate and its confidence interval; the planning figures instead show how sample-size requirements would change under specified assumptions. The registry record does not report whether these illustrative assumptions match the sponsor's original design planning.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.265; treatment proportion p₁ = 0.429; average p̄ = 0.347.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6730 = 1.3191.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6630 = 0.5580.
4. n = (1.3191 + 0.5580)² / (0.1639)² = 131.2, rounded up to 132 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.264705882352941                          # control proportion
p1 <- 0.428571428571429                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3100942)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 132 (80% power), 176 (90% power)
 75% of observed effect: n per arm = 228 (80% power), 304 (90% power)
 50% of observed effect: n per arm = 496 (80% power), 663 (90% power)
power.prop.test: 131.2 
Simulated power at n = 132 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's primary comparisons use the Cochran-Mantel-Haenszel method and report differences in response rates with 95% confidence intervals and p-values. The unadjusted recalculations compare the posted response counts and denominators directly. They are useful as a transparent check on the general direction and uncertainty of the simple group contrast, but they do not reproduce the sponsor's adjusted method.

For each primary comparison, the sponsor-reported interval includes zero. The unadjusted recalculated intervals also include zero. The point estimates differ somewhat because the calculations are not identical; that is not, on its own, evidence of a contradiction. The registry record identifies no discrepancy between the sponsor's analysis and the recalculations.

For secondary continuous outcomes, the sponsor reports MMRM estimates, while recalculations use posted summary statistics and approximate standard deviations derived from standard errors. Model-based estimates can differ from simple summary-statistic calculations because they use different methods and potentially different information. The sponsor's reported analysis is the appropriate reference for what the trial analysis found; recalculations are supplementary and should not be presented as its replacement.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical comparisons are considered. This trial reports a primary response endpoint and multiple secondary outcomes at different assessment times, with comparisons between active-treatment groups and placebo. When many hypotheses are tested, the chance of at least one apparently notable result can increase. A prespecified multiplicity strategy can control that risk, but one is not reported in the registry record. The posted secondary p-values therefore should not be read as if they were isolated confirmatory tests.

The primary endpoint is the principal outcome for interpreting the Week 12 comparison. The registry reports three sponsor comparisons against placebo, but does not report whether or how the testing sequence or family-wise error rate was controlled. The exact inferential status of those multiple primary-treatment comparisons is consequently not fully described in the registry record.

For the primary endpoint, the Full Analysis Set included randomized participants who received at least one dose of study drug and had available data. This description is not identical to an all-randomized analysis population, because it excludes participants without a dose and specifies available data. The registry does not report detailed missing-data methods for the Week 12 endpoint, including how missing responses were classified or whether sensitivity analyses were conducted.

The secondary outcomes are reported as changes from baseline, with MMRM identified for the sponsor comparisons. MMRM can use repeated observations under its modelling assumptions, but the registry does not provide the full model specification or its assumptions about missing observations. Whether those assumptions were examined through sensitivity analyses is not reported in the registry record.

These gaps do not establish that the analyses were inappropriate; they limit what can be independently assessed from the posted record. Interpretation should distinguish the results that are reported from analysis details that are not reported in the registry record.

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: breast cancer (8.3%), gastrooesophageal reflux disease (2.8%), rheumatoid arthritis (2.8%), acute coronary syndrome (2.7%), pancreatitis acute (2.7%).

The registry lists serious adverse events and other adverse events for each displayed treatment group. For the active groups, serious adverse events affected 3 of 37 participants in the lanraplenib group, 5 of 38 in the filgotinib group, and 1 of 39 in the tirabrutinib group. In the placebo-controlled period, serious adverse events affected 2 of 36 participants in the placebo group. The record also lists later placebo-to-active groups, with serious adverse events affecting 0 of 10, 1 of 12, and 0 of 10 participants in the respective groups.

Other adverse events were recorded for 30 of 37, 31 of 38, and 32 of 39 participants in the lanraplenib, filgotinib, and tirabrutinib groups. The placebo-controlled-period figure was 23 of 36. The later placebo-to-active group figures were 10 of 10, 10 of 12, and 7 of 10. No deaths are listed in any displayed group.

These are descriptive event counts. The record's group labels include different treatment periods, and the figures should not be treated as direct comparative estimates of risk without accounting for exposure and follow-up. The most frequent serious-event terms listed in the record include breast cancer, gastrooesophageal reflux disease, rheumatoid arthritis, acute coronary syndrome, pancreatitis acute, and suicidal ideation. The registry summary does not establish that any listed event was caused by a study drug.

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

The primary results answer a narrow statistical question: how often participants met a protocol-defined composite response at Week 12 in each study group, and how the response rates compared with placebo. The active-group response percentages were numerically higher than the placebo percentage, but the sponsor-reported confidence intervals for the differences include zero. The estimates therefore remain compatible with no difference as well as with differences in either direction.

This does not establish that an active treatment is effective, nor does it establish that the treatments have no effect. A lack of clear separation in these estimates is not proof of equivalence. Equivalence or non-inferiority requires a design and analysis that address those questions, and such a claim is not reported in the registry record.

The endpoint also has limits of scope. It requires a particular combination of improvement in participant-reported measures and an hsCRP condition. Results for this composite do not necessarily describe every symptom, disease feature, or outcome that matters to participants. The secondary ESSDAI and ESSPRI outcomes add context, but their uncertainty and the absence of a reported multiplicity strategy make them insufficient grounds for stronger conclusions.

The findings apply to the analysis population described in the registry record: randomized participants who received at least one dose and had available data. The posted record does not give all details needed to assess missing data, model assumptions, or the full analysis plan. These limitations do not erase the reported results, but they constrain the strength and breadth of conclusions that can be drawn from them.

Safety figures are likewise descriptive summaries for the listed groups. They show recorded serious and other adverse events, but do not by themselves establish comparative safety or causation. The record should be read as reporting outcomes from a completed phase 2 study, not as a standalone basis for treatment decisions.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a statistically persuasive difference are not the same thing. The active groups had higher observed Week 12 response percentages than placebo, but the sponsor-reported confidence intervals include zero and span a broad range of possible differences. Reading the point estimates without their uncertainty would overstate how precisely the comparisons are known.

It also shows the importance of endpoint definition. The primary response is not simply a change in one symptom: it combines several participant-reported measures with an hsCRP condition. That construction can make the result clinically interpretable as a specified response pattern, while also making clear that the endpoint does not capture every possible treatment effect.

The record provides a useful contrast between sponsor-reported methods and simple recalculations. The sponsor uses the Cochran-Mantel-Haenszel method for the primary response comparisons and MMRM for listed continuous secondary comparisons. Recalculations based on summary statistics can help readers understand the basic data, but they cannot recreate all features of the sponsor's analyses. Keeping those roles separate is essential for transparent interpretation.

Finally, the study highlights the inferential limits of multiple secondary outcomes and incomplete reporting of analysis details. Without a reported multiplicity strategy, full missing-data methods, and original sample-size justification, readers should focus on the estimates and their uncertainty rather than treating individual p-values as definitive. Such distinctions are central to careful interpretation of clinical-trial evidence.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important design and analysis details unspecified. The original sample-size justification, including the effect the trial was designed to detect, is not reported in the registry record. The planning illustrations based on observed effects should not be mistaken for the trial's original power calculation.

For the primary endpoint, the Full Analysis Set description includes participants with available data, but the handling of missing Week 12 observations is not reported in the registry record. The complete statistical analysis plan, details of randomization and any stratification factors, and the full implementation of the Cochran-Mantel-Haenszel analysis are also not reported. These omissions limit independent assessment of how the reported comparisons were produced.

The registry reports MMRM for listed continuous secondary comparisons, but does not report the model specification, covariance structure, or missing-data assumptions. Several outcomes and times are assessed, while a multiplicity adjustment strategy is not reported in the registry record. Secondary results should therefore be interpreted cautiously.

The secondary comparison entries shown do not include every treatment group for each listed outcome. The reason is not reported in the registry record. In addition, the posted active-treatment durations differ, and the placebo group transitions to rerandomized active treatment after Week 24. Later group safety summaries are not direct substitutes for a contemporaneous placebo comparison.

Finally, the unadjusted continuous-outcome recalculations use approximate standard deviations derived from reported standard errors. They are illustrative rather than exact reproductions of participant-level analyses. The registry record does not provide enough detail to resolve these limitations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess Safety and Efficacy of Filgotinib, Lanraplenib and Tirabrutinib in Adults With Active Sjogren's Syndrome — NCT03100942.
• Registry record last updated 2020-10-23; status last verified 2020-10.
• Results first posted 2020-01-22.
• 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

NCT03100942 is a completed randomized, double-blind, parallel-group phase 2 study of filgotinib, lanraplenib, and tirabrutinib in adults with active Sjogren's syndrome. The primary endpoint was the percentage meeting a composite response definition at Week 12. The registry reports response percentages of 42.9% for lanraplenib, 43.2% for filgotinib, 35.1% for tirabrutinib, and 26.5% for placebo.

The sponsor-reported differences versus placebo have 95% confidence intervals that include zero. Secondary measures assess ESSDAI and ESSPRI changes at Week 12 and Week 24. The registry also lists adverse-event counts, including no deaths in the displayed groups. Missing-data handling, the original sample-size justification, and several details of the analysis plan are not reported in the registry record.