An Active Treatment Study to Induce Clinical Response and/or Remission With GSK1605786A in Subjects With Crohn's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Active Treatment Study to Induce Clinical Response and/or Remission With GSK1605786A in Subjects With Crohn's Disease (NCT01536418), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Clinical Response at Week 12.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group active-treatment study of GSK1605786A in participants with moderately-to-severely active Crohn’s disease. It was sponsored by GlaxoSmithKline. The registry lists enrollment as 255 and describes two assigned oral dosing schedules: 500 milligrams once daily and 500 milligrams twice daily, each for 12 weeks. The study was intended to evaluate induction of clinical response and/or remission. Its planned primary objective was clinical response and/or remission at Week 12, with the response definition based on a CDAI decrease of at least 100 points and remission defined by a CDAI score below 150.

The registry lists a start date of 2011-11-11 and a primary completion date of 2013-10-17. Its status is TERMINATED. The reason for termination is not reported in the registry record, and the registry record does not establish whether termination affected recruitment, follow-up, or the analysis in a particular way. The original recruitment target and the trial’s own sample-size justification are not reported in the registry record.

The trial’s active-treatment comparison means the observed contrast is between dose schedules, not between GSK1605786A and an untreated or placebo group. Randomization is intended, in general, to support a fair comparison of assigned groups by reducing systematic differences at allocation. Masking is intended, in general, to limit influences on care, assessment, and reporting. The registry identifies randomization and quadruple masking but does not report details of how the random sequence was generated, how assignments were concealed, or which roles were included in the masking description.

The record also lists safety, pharmacokinetic, health-outcome, and additional efficacy objectives. Listed secondary measures include remission and response at specified visits, changes in C-reactive protein and faecal calprotectin, pharmacokinetics, and pharmacogenetic analyses. The registry record contains six posted secondary analyses. The extent to which these objectives were completed or used to inform decisions is 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent-to-Treat (ITT) population comprised of all participants who have satisfied the eligibility criteria and were assigned with study medication.

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 Percentage of Participants Achieving Clinical Response at Week 12, measured over At Week 12.

The primary endpoint is the percentage of participants achieving clinical response at Week 12. Response is defined as a decrease from baseline in the Crohn’s Disease Activity Index (CDAI) of at least 100 points. Baseline is defined as Week 0. CDAI combines participant-reported symptoms and investigator-recorded assessments into a disease-activity score. The registry describes symptom domains that include stool frequency, abdominal pain, general well-being, Crohn’s disease symptoms, antidiarrhoeal medication use, abdominal mass, anemia, and weight. A higher score indicates more severe disease.

A threshold-based endpoint turns a change in a multi-component score into a binary outcome: each participant is classified as a responder or non-responder under the stated rule. The percentage then expresses the share of the analysis population classified as responders. In general, this form is straightforward to interpret as the frequency of meeting a defined response criterion, but it does not show the size of score changes among responders or non-responders. Participants with different score trajectories can fall on the same side of the threshold.

The endpoint is used to assess induction response over the 12-week treatment period. It is distinct from clinical remission, which the registry defines using a CDAI score below 150, and from the separate secondary outcomes measured at other visits. The posted primary result is therefore specific to the Week 12 response definition and the recorded analysis population. It should not be read as a summary of every symptom, laboratory measure, safety outcome, or longer-term result.

7. Results Posted in the Registry

• GSK1605786A 500 mg,Twice Daily: 33.3% (42/126) versus 25.2% (32/127) on control; risk difference 8.1 percentage points (95% CI -3.0 to 19.3), risk ratio 1.32 (0.90–1.95); unadjusted two-proportion z-test p = 0.155.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the binary endpoint represent?

The primary outcome is a percentage of participants with an event, where the event is meeting the clinical-response criterion at Week 12. The underlying classification is binary: a participant either meets the stated CDAI decrease threshold or does not. The registry reports the resulting percentages separately for each dosing group. The posted responder counts and group sizes are 32 of 127 for once-daily dosing and 42 of 126 for twice-daily dosing.

In general, binary outcomes are often summarized using a proportion in each group and a contrast between those proportions. A risk difference subtracts the comparator-group proportion from the intervention-group proportion. It expresses the absolute contrast on a proportion scale; unlike a relative measure, it is not a ratio. The recalculated estimate is 0.081 for twice-daily versus once-daily dosing. This is an unadjusted comparison derived from the posted group summary statistics, not a reported adjusted model. The registry does not report an adjustment set for the primary comparison.

What does the confidence interval communicate?

In general, a confidence interval describes uncertainty around an estimate under the assumptions of the method used to calculate it. The recalculated 95% interval for the risk difference runs from -0.030 to 0.193. Because the interval spans zero, it includes values corresponding to no difference as well as values on either side of zero. The interval’s breadth conveys that the observed comparison does not pin down a narrow range of plausible differences. A confidence interval is not a guarantee that the true value lies within the particular calculated limits, and it is not a range containing a stated percentage of individual participant outcomes.

How should the p-value be read?

The recalculated unadjusted p-value is 0.155. In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions were correct. It does not measure effect size, clinical importance, or the chance that a treatment hypothesis is true. The registry does not report a multiplicity plan or a prespecified significance threshold for this primary analysis, so interpretation should not assume that the unadjusted p-value was the sole decision criterion.

What is the sponsor’s reported statistic?

The registry lists a sponsor analysis as “Mean Difference (Final Values),” with an estimate of 8.1 and a 95% confidence interval from -3.0 to 19.3. The method field and p-value are not reported in the registry record. The endpoint result is a percentage meeting a response definition, while the sponsor’s statistic is labeled as a mean difference in final values. The record does not provide enough detail to equate the two calculations or to infer a model beyond the label. Both reported intervals include zero, but their scales and stated measures should remain distinct.

Why does the analysis population matter?

The primary endpoint description identifies the Intent-to-Treat population as participants who satisfied the eligibility criteria and were assigned study medication. The record also states that missing efficacy data were imputed using “no effect”: missing data were treated as no response or no change in response, and classified as non-response. It further says that a participant with baseline CDAI below 100 was considered a non-responder. These choices affect who is classified as having the event and therefore can affect group percentages and the between-group estimate. The registry does not report the number of missing primary outcomes, the number subject to the baseline rule, or sensitivity analyses under alternative missing-data assumptions.

In general, assigning missing binary outcomes to non-response makes the outcome classification explicit, but it relies on an assumption about the unobserved outcome. It is not equivalent to recovering the missing response status. If missingness differs between groups or relates to response, this assumption may affect the comparison. The record’s definition clarifies the stated rule, but the absence of details on missingness prevents assessment of how much it influenced the result.

What can be inferred from the reported design?

Randomization and masking are features that can support internal validity in general, but they do not remove uncertainty due to sample size, missing data, measurement choices, or incomplete reporting. The record identifies a randomized, quadruple-masked, parallel-group design and an active-treatment comparator. It does not report the sequence-generation procedure, concealment method, masking roles, analysis model, or whether the comparison was adjusted for any covariates. Those details are not reported in the registry record and should not be inferred from the design labels alone.

The recalculation is explicitly unadjusted and uses the posted response summaries. It is useful as a transparent comparison of the displayed group results, but it does not replace an analysis that may have used additional prespecified methods. Since the discrepancy indicator is false, the posted sponsor estimate does not conflict materially with the recalculated numerical comparison. The sponsor’s analysis remains a separately labeled result, with limited methodological detail in the record.

10. Confidence Intervals and Precision

The recalculated risk difference for twice-daily versus once-daily dosing is 0.081, and its 95% confidence interval extends from -0.030 to 0.193. The interval is important because it shows uncertainty in the comparative estimate, not just the direction of the point estimate. Its lower limit is below zero and its upper limit is above zero, so the data are compatible with a range that includes no difference and with differences in either direction under the calculation used.

In general, a confidence interval’s width reflects both the observed data and the method’s assumptions. A broader interval means less precision about the size and direction of the effect than a narrower interval would. The interval is not concentrated on a single value, and the estimate should not be described as a precisely established advantage for either schedule. The arm percentages, 25.2% and 33.3%, are observed summaries; they do not on their own capture uncertainty in the comparison.

The sponsor’s reported estimate is 8.1, with a 95% confidence interval from -3.0 to 19.3. That interval also includes zero. The sponsor’s statistic is labeled as a mean difference in final values, so its scale is not explicitly described as the recalculated risk-difference scale. The registry record does not report the sponsor method or p-value. Similar displayed directions and intervals do not erase the distinction between the stated measures.

Precision also depends on outcome definition and missing-data handling. The response threshold classifies participants by whether they achieved a CDAI decrease of at least 100 points; the result does not convey the distribution of score changes. The record specifies non-response imputation for missing efficacy data, but does not report how many primary outcomes were missing or the result under alternative assumptions. Those omissions limit assessment of the robustness of the interval and point estimate.

11. 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 illustrations based on the observed effect, not the original trial’s design calculation. 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 at the stated fraction of the observed effect. For this binary-outcome comparison, the planning figures are participants per arm, not total events.

Under planning for 100% of the observed effect, the illustration gives 490 participants per arm for 80% power and 656 participants per arm for 90% power. Planning for 75% of the observed effect gives 854 participants per arm for 80% power and 1,142 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,879 participants per arm for 80% power and 2,514 participants per arm for 90% power.

In general, a power target describes the long-run chance of detecting an effect of the specified size under the assumed design and statistical model, if that effect is the true one. The 80% power column and the 90% power column therefore represent alternative planning targets: the latter requires a larger planned group size under the stated assumptions. The illustration also shows that smaller effects need more participants to detect, because they are harder to distinguish from sampling variation.

These planning numbers are not observed power. They do not describe the probability that this completed trial detected an effect after its results were known. The original sample-size justification and design assumptions are not reported in the registry record, so the illustration should not be read as the trial’s planned recruitment target or as evidence about why the study was terminated.

12. 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 = 0.252; treatment proportion p₁ = 0.333; average p̄ = 0.293.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6434 = 1.2611.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6409 = 0.5394.
4. n = (1.2611 + 0.5394)² / (0.0814)² = 489.7, rounded up to 490 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 <- 0.251968503937008                          # control proportion
p1 <- 0.333333333333333                          # 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(1536418)
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 = 490 (80% power), 656 (90% power)
 75% of observed effect: n per arm = 854 (80% power), 1,142 (90% power)
 50% of observed effect: n per arm = 1,879 (80% power), 2,514 (90% power)
power.prop.test: 489.7 
Simulated power at n = 490 per arm: 0.799 (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.

13. Analyses Reported by the Sponsor

The registry’s sponsor analysis reports a mean difference in final values of 8.1, with a 95% confidence interval from -3.0 to 19.3. The recalculated unadjusted risk difference is 0.081, with a 95% confidence interval from -0.030 to 0.193. The discrepancy indicator is false, so the posted sponsor estimate and the recalculation do not show a flagged numerical disagreement.

The measures should nevertheless be described by their own labels. The primary endpoint is the percentage achieving clinical response, and the recalculation contrasts the response proportions. The sponsor statistic is labeled “Mean Difference (Final Values).” The registry does not report the sponsor’s analysis method or p-value, so it is not possible to establish from the record whether its estimate used the same outcome coding, scale, or calculation as the unadjusted recalculation.

Both confidence intervals include zero. That shared feature indicates that neither interval excludes a null contrast, but it does not make the estimates interchangeable. The sponsor’s result is the analysis recorded by the sponsor; the recalculation is a simple, unadjusted comparison of the posted group summaries. Interpret the recalculation as a transparent descriptive check, not as a replacement for undocumented sponsor methods.

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint of clinical response at Week 12 and lists secondary outcomes covering remission and response at specified visits, changes in C-reactive protein and faecal calprotectin, pharmacokinetics, and pharmacogenetic analyses. It records six posted secondary analyses. When multiple outcomes or time points are examined, the chance of at least one apparently notable result can increase in general. Statistical approaches to multiplicity can address that issue, but the trial’s multiplicity strategy is not reported in the registry record.

The registry record also does not report whether an interim analysis was planned or conducted, what testing hierarchy applied, or which analyses were designated confirmatory. These details should not be inferred from the existence of primary and secondary outcome listings. The unadjusted recalculated p-value is 0.155, but no claim about multiplicity-adjusted inference can be made without a stated procedure.

The primary endpoint description says the Intent-to-Treat population comprises participants who satisfied eligibility criteria and were assigned study medication. It specifies “no effect” imputation for missing efficacy data: missing data were treated as no response or no change in response and classified as non-response. It also specifies that a participant with baseline CDAI below 100 was considered a non-responder. These are relevant classification rules for the primary efficacy endpoint.

The number of missing primary outcome observations, their distribution by group, and the results of sensitivity analyses are not reported in the registry record. Methods used for missing secondary outcomes are also not reported in the registry record. In general, missing-data assumptions can matter because observed outcomes may differ systematically from unobserved outcomes. A non-response assignment is a defined analysis rule, not evidence that every missing participant would in fact have failed to respond.

The posted information does not identify a separate per-protocol population or explain whether deviations from assigned treatment affected inclusion. The primary endpoint population is described, but the handling of all analysis populations and the sponsor’s detailed statistical plan are not reported in the registry record. This limits the ability to assess the full prespecification, robustness, and multiplicity context of the efficacy findings.

15. 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: bronchitis (0.8%), cellulitis (0.8%), tonsillitis (0.8%), cardiac failure (0.8%), crohn's disease (0.8%).

The registry reports serious adverse events for 8 participants in the once-daily group and 6 participants in the twice-daily group. The corresponding groups at risk are 127 and 126. Deaths are reported as 0 in each group. These figures describe the recorded serious-adverse-event counts during the study; they do not establish whether any event was caused by study treatment.

Other adverse events are reported for 61 participants in the once-daily group and 57 participants in the twice-daily group, with 127 and 126 participants at risk, respectively. The registry lists bronchitis, cellulitis, tonsillitis, cardiac failure, Crohn’s disease, and musculoskeletal chest pain among the top serious adverse-event terms, each at 0.8%. These listed terms are not accompanied in the record by a group-specific count in the information available for interpretation.

In general, safety counts require context about how events were defined, collected, and attributed, as well as treatment exposure and follow-up. The record gives group counts and the listed terms, but it does not report detailed event timing, severity grading beyond the serious-event classification, relatedness assessments, or the reason for study termination. Differences in counts alone should not be interpreted as proof of a safety difference, particularly without additional analysis and context.

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

The main statistical observation is that the Week 12 clinical-response percentage was 25.2% with GSK1605786A 500 mg once daily and 33.3% with GSK1605786A 500 mg twice daily. The unadjusted recalculated risk difference is 0.081. Its 95% confidence interval, from -0.030 to 0.193, includes zero and covers values on both sides of no difference. The result therefore leaves meaningful uncertainty about the comparative response proportions in this study.

This is an active-treatment comparison between dose schedules. It does not estimate the effect of either schedule versus placebo or no treatment. It also does not answer whether participants achieved clinical remission, whether any response persisted beyond Week 12, or how the groups compared on all secondary outcomes. Those questions require their own results and definitions; their full interpretation is not established by the primary endpoint comparison.

The endpoint records whether a participant crossed a CDAI change threshold. It does not show the magnitude or pattern of score changes for every participant. The posted response proportions should be read as summaries under the registry’s classification rules, including the specified treatment of missing efficacy data as non-response and the baseline CDAI rule. The number of missing outcomes and the effect of alternative assumptions are not reported in the registry record.

The sponsor’s reported mean difference in final values is 8.1, with a 95% confidence interval from -3.0 to 19.3. Its interval also includes zero. The record does not report the sponsor analysis method or p-value, so this result cannot be used to fill in methodological details that are absent from the registry. The estimate is separately labeled from the recalculated risk difference.

The registry status is TERMINATED, but the reason is not reported in the registry record. Without that information, termination should not be used to infer the cause, the quality of the data, or the direction of any bias. Overall, the record documents an observed numerical difference between the assigned groups, but the uncertainty, endpoint scope, active comparator, and incomplete reporting constrain what can be concluded from it.

17. Why This Trial Matters Statistically

This trial illustrates why a difference in observed percentages is not enough to establish a clear comparative effect. The twice-daily group had a higher posted Week 12 response percentage than the once-daily group, yet the recalculated confidence interval includes zero and extends to values in both directions. The point estimate communicates the observed contrast; the interval communicates how uncertain its size and direction remain under the calculation used.

It also demonstrates the importance of identifying the estimand and scale. A response proportion is a binary summary based on a CDAI threshold. The recalculated risk difference compares those proportions, while the sponsor result is labeled as a mean difference in final values. Even when numerical estimates appear similar, their labels and underlying quantities matter. Clear reporting of the outcome, analysis method, and units is essential for valid comparison.

Missing-data rules are another important part of an endpoint, not a minor technical footnote. The record explicitly treats missing efficacy data as non-response and applies a non-responder classification to participants with baseline CDAI below 100. Such rules shape the observed analysis result. Without counts of missing observations or sensitivity analyses, readers cannot assess how much alternative assumptions might change the interpretation.

The record further shows the limits of interpreting a trial with multiple outcomes when multiplicity methods are not reported. It lists a primary endpoint and several secondary measures, but does not describe a testing hierarchy or correction strategy. In general, that context affects how an isolated p-value should be viewed. Finally, the active-treatment design answers a dose-schedule comparison question, not whether the study drug is better than no active treatment. Stating the question precisely is necessary for keeping conclusions within the scope of the design and data.

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

The registry record identifies the study as terminated but does not report the reason. That missing context limits interpretation of the trial’s completion and any potential effects of termination on recruitment, follow-up, or planned analyses. The record lists enrollment as 255, while the primary endpoint group sizes are 127 and 126; it does not explain the relationship between those figures or provide a disposition account for all enrolled participants.

The sponsor’s statistical method and p-value are not reported in the registry record. The sponsor estimate is labeled as a mean difference in final values, but the record does not provide the scale details or analysis specification needed to determine how it relates exactly to the binary response endpoint. The recalculation is unadjusted, and no covariate-adjusted primary estimate is reported in the available record.

Although the registry describes randomization and quadruple masking, it does not report sequence generation, allocation concealment, masking roles, or details of treatment adherence and exposure. These omissions make it difficult to assess implementation from the registry record alone. The primary endpoint description specifies how missing efficacy data were classified, but the missing-outcome count, group distribution, and sensitivity analyses are not reported.

The record lists multiple secondary outcomes and analyses but does not report the multiplicity strategy, interim-analysis plans, or the trial’s complete statistical analysis plan. The registry describes clinical response at Week 12, but the summary of the primary comparison does not provide score distributions or a fuller account of the response trajectory. Secondary outcome results are not detailed in the record excerpt beyond the listed outcome topics and count of analyses.

Finally, both groups received active treatment, so the study does not provide a placebo or no-treatment contrast. Its primary endpoint is a threshold-based response measure at a single specified visit, and the registry’s status and reporting detail constrain broader conclusions about durability, comparative benefit in other settings, or outcomes beyond those recorded.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Active Treatment Study to Induce Clinical Response and/or Remission With GSK1605786A in Subjects With Crohn's Disease — NCT01536418.
• Registry record last updated 2018-01-29; status last verified 2018-01.
• Results first posted 2017-08-17.
• 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 randomized, quadruple-masked, parallel-group Phase 3 active-treatment study of GSK1605786A in moderately-to-severely active Crohn’s disease. The dosing comparison was 500 milligrams once daily versus 500 milligrams twice daily for 12 weeks. The record lists enrollment as 255 and status as TERMINATED; the reason for termination is not reported in the registry record.

The primary endpoint was clinical response at Week 12, defined as a CDAI decrease from baseline of at least 100 points. The posted response percentages were 25.2% for once-daily dosing and 33.3% for twice-daily dosing. The unadjusted recalculated risk difference was 0.081, with a 95% confidence interval from -0.030 to 0.193 and p = 0.155. The sponsor-reported mean difference in final values was 8.1, with a 95% confidence interval from -3.0 to 19.3.

Both intervals include zero. Interpretation is limited by the active-treatment comparator, threshold-based endpoint, unspecified multiplicity strategy, and missing details on the sponsor’s analysis method and missing-outcome sensitivity analyses.