Study of LX3305 in Subjects With Active Rheumatoid Arthritis on Stable Methotrexate: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of LX3305 in Subjects With Active Rheumatoid Arthritis on Stable Methotrexate (NCT00903383), a randomized phase 2 study. The primary outcome is ACR20 Response at Week 12.

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 2, randomized, parallel-group, placebo-controlled study. Its official title describes a multi-center, double-blind, multiple-dose design; the masking field identifies quadruple masking. Participants with active rheumatoid arthritis on stable methotrexate therapy were assigned to one of three daily oral LX3305 dose groups or to matching placebo. The arm descriptions specify a 12-week dosing period.

The registry reports enrollment of 208. The posted primary outcome lists the Intent to Treat Population. Outcome summaries give the number of participants in each arm used for that measure: 55 in the low-dose group, 54 in the mid-dose group, 50 in the high-dose group, and 49 in the placebo group. These arm-level figures are presented as posted; the registry record does not explain any differences between enrollment and the analysis populations.

The study status is completed. The registry reports a start date of 2009-07 and a primary completion date of 2010-09. It identifies Lexicon Pharmaceuticals as sponsor. The brief summary describes the purpose as evaluating safety, tolerability, and effectiveness of LX3305 versus placebo in participants with active rheumatoid arthritis receiving stable methotrexate therapy.

The posted results focus on response at Week 12, along with secondary clinical and laboratory outcomes. The registry record does not report the intended allocation ratio, details of the randomization procedure, the concealment procedure, or the original statistical analysis plan. The design fields describe the broad study structure, but they do not establish how every aspect of trial conduct or analysis was implemented.

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: There was a 4 week screening period prior to the 12-week treatment period.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat Population

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 ACR20 Response at Week 12, measured over Baseline and 12 weeks.

The primary endpoint is the number of participants with an ACR20 response at Week 12, assessed from baseline through 12 weeks. ACR20 is a composite response definition: it requires at least 20% improvement in swollen joint count, at least 20% improvement in painful or tender joint count, and at least 20% improvement in at least 3 of these assessments: the participant’s assessment of pain, global assessment of disease activity, assessment of physical function, or an acute phase reactant—C-reactive protein or erythrocyte sedimentation rate.

A response definition combines several dimensions of disease assessment rather than relying on a single measure. Requiring improvement in joint counts and in additional assessments means that an ACR20 response represents a specified pattern of change across the included measures. Reporting the number meeting that definition makes the endpoint interpretable as a binary outcome: each participant either meets the response criteria or does not.

This endpoint was used to evaluate efficacy in participants receiving stable methotrexate therapy. The registry record identifies the Intent to Treat Population for the primary outcome. It does not give further detail about how missing component measurements or missing Week 12 assessments were handled.

7. Results Posted in the Registry

• Low Dose: 43.6% (24/55) versus 49.0% (24/49) on control; risk difference -5.3 percentage points (95% CI -24.5 to 13.8), risk ratio 0.89 (0.59–1.35); unadjusted two-proportion z-test p = 0.585.
• Mid Dose: 40.7% (22/54) versus 49.0% (24/49) on control; risk difference -8.2 percentage points (95% CI -27.4 to 10.9), risk ratio 0.83 (0.54–1.28); unadjusted two-proportion z-test p = 0.401.
• High Dose: 60.0% (30/50) versus 49.0% (24/49) on control; risk difference 11.0 percentage points (95% CI -8.5 to 30.5), risk ratio 1.23 (0.85–1.76); unadjusted two-proportion z-test p = 0.271.

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.

ACR50 Response at Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Low Dose: 10.9% (6/55) versus 24.5% (12/49) on control; risk difference -13.6 percentage points (95% CI -28.2 to 1.0), risk ratio 0.45 (0.18–1.10); unadjusted two-proportion z-test p = 0.068.
  • Mid Dose: 9.3% (5/54) versus 24.5% (12/49) on control; risk difference -15.2 percentage points (95% CI -29.5 to -0.9), risk ratio 0.38 (0.14–1.00); unadjusted two-proportion z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Mid Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

ACR70 Response at Week 12

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Low Dose: 3.6% (2/55) versus 6.1% (3/49) on control; risk difference -2.5 percentage points (95% CI -10.8 to 5.9), risk ratio 0.59 (0.10–3.41); unadjusted two-proportion z-test p = 0.554.
  • Mid Dose: 7.4% (4/54) versus 6.1% (3/49) on control; risk difference 1.3 percentage points (95% CI -8.4 to 11.0), risk ratio 1.21 (0.28–5.14); unadjusted two-proportion z-test p = 0.796.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose 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 Mid Dose and the control. The interval gives the range of effects that remain compatible with the data.

Hybrid ACR Response 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 deviations.
• Result:
  • Low Dose: mean 26.59 versus 35.29 on control; difference -8.70 (95% CI -17.89 to 0.50), standardized effect d = -0.37; z-test p = 0.064.
  • Mid Dose: mean 27.42 versus 35.29 on control; difference -7.87 (95% CI -17.30 to 1.56), standardized effect d = -0.32; z-test p = 0.102.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose 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 Mid Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover response thresholds, a hybrid response measure, and changes in inflammatory laboratory measures. Together, they offer different views of clinical response and biological measurement, rather than repeating the primary endpoint in identical form. The posted summaries include ACR50 and ACR70 responses and Hybrid ACR response; the registry also lists changes from baseline in C-reactive protein and erythrocyte sedimentation rate. The record contains no posted results for the laboratory change outcomes in the registry record for this analysis.

Across the available secondary summaries, results do not establish a uniform pattern that would remove the uncertainty in the primary ACR20 comparisons. The secondary outcomes use different definitions and scales, so their estimates are not interchangeable with the ACR20 risk differences. They may help describe the broader pattern of observed outcomes, but they do not by themselves confirm or overturn the primary comparison.

Unadjusted secondary results carry less weight because several outcomes and comparisons create multiple opportunities for apparently notable results. Unless a testing strategy accounts for that multiplicity, the chance of at least one unusual result across the set can be greater than for a single prespecified comparison. This is a general statistical concern, not evidence that any particular secondary result is false. The registry record does not report a multiplicity adjustment, a hierarchy among outcomes, or sponsor-reported analyses for these endpoints.

The secondary outcomes are therefore best treated as descriptive or exploratory evidence in the context of the posted record. They can inform questions for further evaluation, but the available record does not establish that they were intended or analyzed as confirmatory endpoints.

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

• ACR50 Response at Week 12
• ACR70 Response at Week 12
• Hybrid ACR Response at Week 12
• Change From Baseline in C-reactive Protein (mg/L) at Week 12
• Change From Baseline in Erythrocyte Sedimentation Rate (mm) at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either met the ACR20 response definition at Week 12 or did not. For a binary endpoint, a group response proportion describes the fraction of participants who met the criteria. Comparisons can be expressed as risk differences, which subtract the comparator-group proportion from the intervention-group proportion. A risk difference of zero represents equal observed proportions. A negative estimate indicates a lower observed proportion in the intervention group; a positive estimate indicates a higher observed proportion.

What does the confidence interval describe?

A confidence interval expresses uncertainty around an estimated contrast. In general, it shows a range of values compatible with the observed data under the statistical method used. A wide interval indicates less precision than a narrow interval. For a risk difference, an interval that includes zero does not rule out equal group proportions; it also leaves room for differences in either direction. The primary comparison intervals all include zero, and their endpoints extend meaningfully in both directions. That makes the direction and size of the underlying difference uncertain.

How should the p-values be read?

A p-value describes how surprising data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It does not give the probability that the null hypothesis is true, the probability that a result occurred by chance, or the size of an effect. The primary comparison p-values are identified as unadjusted. They should be read alongside the estimates and confidence intervals, rather than as stand-alone declarations. The registry record does not report a sponsor analysis method or a multiplicity procedure for these comparisons.

Why compare each dose with placebo?

The parallel-group design assigns participants to separate dose or placebo arms. The posted primary comparisons contrast each LX3305 dose with placebo, preserving the dose-specific view of the results. This is different from combining dose groups into one intervention group: the registry record does not report such a pooled primary comparison. The three estimates have different signs and different degrees of uncertainty, so an overall summary should not obscure that variation.

What does the registry say about the analysis?

The primary outcome identifies the Intent to Treat Population, but the record does not describe the precise analysis procedure, missing-data rules, covariate adjustment, or handling of participants without an observed Week 12 outcome. No sponsor-reported analyses are listed for the outcomes. Consequently, the posted summaries support descriptive comparisons and the stated unadjusted comparisons, but do not document the full statistical workflow behind them.

What do the planning calculations represent?

General sample-size planning asks how many participants would be needed to detect a prespecified difference under stated assumptions. The planning illustrations accompanying the posted comparisons use the observed effect as a reference and also consider fractions of that effect. Smaller target effects generally require more participants because they are harder to distinguish from ordinary sampling variation. These calculations are not evidence that the original trial was designed around those assumptions; the original sample-size justification is not reported in the registry record.

The posted planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For outcomes other than time-to-event outcomes, the figures are participants per arm. This study’s posted primary outcome is binary, so the planning figures should be understood as per-arm illustrations for a two-group comparison, not as a reconstruction of the original design. The registry record does not report whether the original study used the same assumptions or method.

General interpretation also depends on how outcomes were measured and analyzed. ACR20 is a composite threshold, so its binary summary does not retain the full range of changes in each component. The registry’s secondary outcomes provide other perspectives, but they do not replace the primary endpoint. Agreement or disagreement across endpoints can be informative, yet different outcomes may have different scales, variability, and susceptibility to missing data. The record does not report enough analytic detail to determine how those issues were handled.

11. Confidence Intervals and Precision

The risk-difference confidence intervals provide a direct view of precision for the primary comparisons. For low dose versus placebo, the estimate is -0.053, and the 95% confidence interval runs from -0.245 to 0.138. For mid dose versus placebo, the estimate is -0.082, with an interval from -0.274 to 0.109. For high dose versus placebo, the estimate is 0.110, with an interval from -0.085 to 0.305.

All three intervals include zero. In general, this means the data do not pin down a nonzero risk difference at the confidence level represented by these intervals. The intervals also extend across values on both sides of zero, so the observed data remain compatible with lower or higher response proportions in the LX3305 group relative to placebo. The point estimates alone are not sufficiently precise to settle the direction of the contrast.

The intervals are broad in relation to their point estimates, indicating substantial uncertainty about the size of each difference. The relatively modest arm-level outcome counts are part of the context for reading this uncertainty, although the registry record does not give a formal precision target or the original sample-size rationale. Confidence intervals describe statistical uncertainty under the calculation method; they do not account for every possible limitation, such as unreported missing-data decisions or outcome-assessment issues.

Precision should therefore be considered separately from the observed direction. The high-dose estimate is positive, while the other two estimates are negative, but uncertainty remains in every comparison. The posted data do not support treating small differences between point estimates as a reliable ranking of the dose groups.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants, because these are not time-to-event outcomes. The stated planning 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 for the relevant comparison. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under those assumptions for an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column gives the corresponding planning figure for a 90% chance. These are design probabilities under assumptions, not probabilities that the observed result is correct. For example, the high-dose primary comparison gives planning figures of 320 participants per arm for 80% power and 428 participants per arm for 90% power when planning for 100% of the observed effect.

As the target effect is reduced to 75% or 50% of the observed effect, the listed participant requirements rise. This reflects a general statistical principle: smaller differences are more difficult to distinguish from sampling variation, so they typically require larger groups. These figures are planning illustrations, not observed power. They do not indicate the probability that this completed trial detected an effect, and they should not be interpreted as a retrospective test of the trial’s success.

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 = 0.490; treatment proportion p₁ = 0.436; average p̄ = 0.463.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7052 = 1.3821.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7042 = 0.5926.
4. n = (1.3821 + 0.5926)² / (-0.0534)² = 1,365.9, rounded up to 1,366 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 <- 0.489795918367347                          # control proportion
p1 <- 0.436363636363636                          # 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(903383)
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 = 1,366 (80% power), 1,829 (90% power)
 75% of observed effect: n per arm = 2,434 (80% power), 3,258 (90% power)
 50% of observed effect: n per arm = 5,485 (80% power), 7,343 (90% power)
power.prop.test: 1365.9 
Simulated power at n = 1,366 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, with multiple dose-versus-placebo comparisons. When many outcomes or contrasts are examined, the chance of obtaining an apparently unusual result somewhere among them can increase. Statistical approaches such as prespecified testing sequences or adjustment procedures can address that issue, but the registry record does not report whether any such approach was planned or used. The unadjusted p-values should therefore not be treated as if they came from a documented family-wise testing strategy.

The record identifies the Intent to Treat Population for the primary outcome, but does not report detailed population definitions for all analyses. It also does not describe how missing Week 12 measurements, withdrawals, or incomplete ACR components were handled. These omissions matter because binary response classification can depend on how incomplete outcome information is treated. No assumption about the missing-data method can be made from the posted record.

The registry record does not report a full statistical analysis plan, including the planned model, covariate adjustment, treatment of protocol deviations, or the timing and conduct of interim analyses. It lists no reported analyses for the posted outcomes. This limits the ability to determine whether the posted summaries reproduce a prespecified analysis or whether any additional analytical decisions were made.

These are reporting limitations, not proof that the trial lacked procedures for multiplicity, missing data, or analysis conduct. They mean that those procedures cannot be evaluated from the registry record. Interpretation should remain anchored to the posted counts, comparisons, and their uncertainty, without assuming details that are not recorded.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: nausea and vomiting (1.8%), atrial fibrillation (1.8%).

The registry reports serious adverse events affecting 2 participants in the low-dose group, and 0 in the mid-dose, high-dose, and placebo groups. The groups at risk were 55, 54, 50, and 49, respectively. For other adverse events, the posted affected-participant counts were 10 in the low-dose group, 5 in the mid-dose group, 10 in the high-dose group, and 12 in the placebo group. These are counts, not adjusted comparisons of risk.

The registry lists nausea and vomiting and atrial fibrillation as the top serious adverse-event terms, each reported as 1.8%. It does not provide further event-level detail in the available record. Death counts are not reported in the registry record.

These figures describe reported events in the study groups. They do not establish whether an event was caused by a study treatment, and the record does not give enough detail to assess timing, severity beyond the serious-event classification, or the statistical uncertainty around group differences. Event counts should be read descriptively rather than as a definitive comparison of safety.

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

The posted primary results describe how many participants in each group met the ACR20 response criteria at Week 12 and quantify the observed dose-versus-placebo differences. The risk-difference estimates vary in direction across doses, and each confidence interval includes zero. This means the posted estimates are uncertain and do not establish a clear difference between any one LX3305 dose and placebo.

That interpretation is not equivalent to concluding that the groups were identical. The confidence intervals leave room for differences in either direction, and the registry record does not provide a prespecified equivalence or non-inferiority framework. A non-significant unadjusted p-value is not proof of no effect. Likewise, an observed difference is not proof that treatment caused it.

The endpoint is a threshold-based composite. It records whether a participant met the defined response criteria, not the full amount of change in every component. The secondary measures may add context, but their unadjusted nature and the absence of a reported multiplicity strategy make them less conclusive. The record also does not report the detailed handling of missing data or the complete statistical analysis plan.

The trial was completed, and the registry provides results from the stated study groups. Those results are relevant to the study question in participants with active rheumatoid arthritis receiving stable methotrexate, but they should not be generalized beyond the population and 12-week assessment described in the record. The posted information does not justify medical advice or a conclusion about treatment decisions. It supports a statistical reading of the reported outcomes and their precision, with important limits on what can be inferred.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate, a confidence interval, and a p-value answer different questions. The point estimate gives the observed direction and size of a contrast; the confidence interval conveys uncertainty about that estimate; and the p-value summarizes compatibility with a specified null hypothesis under an analysis framework. Looking at only one of these can produce an incomplete reading. Here, the three primary estimates point in different directions and all have intervals that include zero.

The dose-specific presentation also matters. Combining dose groups would conceal the differing observed directions and would require an analysis choice not reported in the registry. Keeping the comparisons separate makes clear that the posted results do not show one uniform pattern across doses.

The record also demonstrates the importance of distinguishing confirmatory from exploratory evidence. Several outcomes are listed, but multiplicity handling and sponsor-reported analyses are not reported. A collection of unadjusted secondary comparisons should not be given the same evidential weight as a single prespecified primary analysis with a documented testing plan.

Finally, registry reporting determines how fully readers can assess trial results. The record states the population, endpoint, arm summaries, and basic study design, while leaving original design assumptions, missing-data handling, and analysis details unreported. Those gaps do not invalidate the posted numbers, but they constrain their interpretation and underline why precision and reporting transparency are central to clinical-trial statistics.

18. 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 primary outcome is assessed at Week 12 after a 12-week dosing period. The record does not provide longer-term outcome results, so the posted endpoint addresses the stated short-term assessment only. The study is Phase 2, and the registry does not report the original sample-size justification. The enrollment and arm-level analysis counts describe the study, but the record does not explain how those analysis counts relate to enrollment or whether any participants lacked outcome measurements.

The primary endpoint is a composite response threshold. A binary response count does not show the distribution of changes in each component, and small shifts around the threshold can affect whether a participant is classified as a responder. The record does not provide component-level results or describe how incomplete component data were handled.

There are three dose comparisons against placebo and multiple secondary outcomes. The registry record does not report a multiplicity strategy, a prespecified hierarchy, or a full statistical analysis plan. It lists no reported analyses for the outcomes. This restricts assessment of whether the displayed comparisons reflect the intended inferential plan.

Safety information is also limited to posted counts and selected serious-event terms. The record does not report deaths, and it does not provide further event-level details in the registry entries. These limitations are specific to what is reported in the registry record; they should not be mistaken for evidence that unreported analyses or procedures did not exist.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of LX3305 in Subjects With Active Rheumatoid Arthritis on Stable Methotrexate — NCT00903383.
• Registry record last updated 2011-12-15; status last verified 2011-11.
• Results first posted 2011-12-15.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed Phase 2, randomized, parallel-group, placebo-controlled, multiple-dose study of daily oral LX3305 for participants with active rheumatoid arthritis receiving stable methotrexate. The dosing period was 12 weeks. The primary outcome was the number of participants meeting ACR20 response criteria at Week 12 in the Intent to Treat Population.

The posted primary counts were 24 of 55 for low dose, 22 of 54 for mid dose, 30 of 50 for high dose, and 24 of 49 for placebo. Each dose-versus-placebo risk-difference confidence interval included zero. The registry also lists secondary response and laboratory outcomes, but does not report a multiplicity procedure, detailed missing-data handling, or a full statistical analysis plan. Serious and other adverse-event counts are reported by arm; death counts are not reported in the registry record.