BOL-303259-X With Timolol 0.5% in Subjects With Open-Angle Glaucoma or Ocular Hypertension: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BOL-303259-X With Timolol 0.5% in Subjects With Open-Angle Glaucoma or Ocular Hypertension (NCT01707381), a randomized phase 2 study. The primary outcome is 24 Hour IOP.

2. Clinical Question

This is a comparison of two active treatments, not a comparison with no treatment or placebo. The question concerns the recorded pressure outcome during the study period. It does not by itself answer how results might differ in other populations, with other treatment durations, or for outcomes that were not measured.

3. Trial Design

The registry describes a completed, randomized, single-center, open-label, phase 2 crossover study. It enrolled 25 participants with open-angle glaucoma or ocular hypertension. In a crossover design, participants receive more than one treatment over the course of a study, so comparisons may involve measurements associated with the same participants under different treatments. The registry does not report the treatment sequence, any washout interval, or the detailed timing of assessments between treatment periods.

The treatment descriptions specify four weeks of dosing for each treatment: BOL-303259-X as one evening drop once daily, and timolol maleate ophthalmic solution 0.5% as one morning drop and one evening drop twice daily. The stated comparison concerns intraocular pressure assessed over a 24-hour period after treatment. The registry lists the study start as 2012-11 and primary completion as 2013-12, and records the study status as completed.

The primary outcome summaries give 21 participants for each treatment group. The registry does not explain the relationship between those outcome counts and the total enrollment of 25, nor does it give a detailed account of exclusions or incomplete assessments. The primary population is described as the Intent to Treat (ITT) Population, with inclusion requiring randomization, at least one dose, a baseline assessment, and at least one postbaseline intraocular assessment.

Randomization helps allocate participants to treatment sequences, but open-label treatment means masking was not used. The registry does not report the randomization procedure, allocation concealment, or detailed crossover sequence. These details matter when assessing the possibility of period, sequence, or carryover effects, but they are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Period 1

Period 2

Analysis population for the primary outcome, as defined in the registry: Intent to Treat (ITT) Population:All randomized subjects who received at least one dose of study drug, had a baseline and at least one postbaseline intraocular assessment.

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: ITT Population: All randomized subjects who received at least one dose of study drug, had a baseline and at least one postbaseline intraocular assessment.

6. Primary Endpoint

The registry lists the primary outcome as 24 Hour IOP, measured over after 4 weeks of treatment.

The primary endpoint is 24-hour intraocular pressure (IOP), measured in mm Hg. The registry describes it as supine IOP measured in the study eye after four weeks of treatment. The stated study question focuses on IOP measured over a 24-hour period, allowing pressure to be considered across the daily cycle rather than at a single assessment time. The registry does not give further detail about the individual measurement times or how they were combined for the primary endpoint.

IOP is a continuous measure: its observed values can vary across a range rather than falling into a small set of categories. The registry reports least-squares means for the treatment groups. Such means are model-based averages and may reflect adjustment for terms in the statistical model; the registry does not identify all model terms. The primary endpoint is useful for quantifying the average pressure level under each treatment and the estimated difference between treatments. It does not describe every participant’s response or the distribution of individual measurements.

The endpoint is specified after four weeks of treatment, so it represents an outcome at that study time point, not a measure of longer-term pressure patterns. It is also a surrogate clinical measurement rather than a direct measure of every outcome relevant to participants. The posted result should therefore be read as a statistical comparison of this defined pressure measure, in the analyzed population and study setting.

7. Results Posted in the Registry

• BOL-303259-X: mean 21.77 versus 23.55 on control; difference -1.78 (95% CI -3.24 to -0.32), standardized effect d = -0.74; z-test p = 0.017.

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.

IOP Area Under the Curve Over 24 Hours

• 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:
  • BOL-303259-X: mean 21.77 versus 23.54 on control; difference -1.77 (95% CI -3.20 to -0.34), standardized effect d = -0.75; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BOL-303259-X than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The two posted secondary outcomes concern 24-hour IOP area under the curve and 24-hour ocular perfusion pressure. The registry reports an analysis for IOP area under the curve, while no result for ocular perfusion pressure is included among the posted secondary outcomes. Across the reported primary and secondary IOP measures, the estimates point in the same direction: the treatment difference is negative for BOL-303259-X relative to timolol. This broad pattern is consistent across the reported pressure measures, but it does not make those endpoints interchangeable.

The secondary outcomes address related but distinct measurements. Agreement in direction can add context to the primary result, but secondary outcomes generally carry less weight because the primary endpoint is the main prespecified question and multiple outcomes create more opportunities for apparently notable findings. The registry does not report whether a multiplicity adjustment was used, whether a hierarchy among outcomes was prespecified, or how secondary results were intended to affect conclusions.

Unadjusted secondary p-values should therefore be interpreted cautiously. When several outcomes are assessed, the chance of at least one apparently unusual result can increase if each is evaluated independently at the same threshold. In general, adjustment procedures or prespecified testing hierarchies can address this issue, but the record does not report such procedures. The secondary estimates are best treated as supportive context rather than as independent confirmation of the primary result.

The registry lists two secondary outcomes, but only one secondary outcome analysis is posted. The result for the other listed outcome is not reported in the registry record. That gap means the overall secondary-outcome pattern cannot be fully assessed from the posted results. The absent result should not be interpreted as a null finding or as evidence of no difference.

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

• 24-hour Ocular Perfusion Pressure
• IOP Area Under the Curve Over 24 Hours

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports analysis of the primary treatment difference by ANCOVA. ANCOVA, or analysis of covariance, compares group means while accounting for one or more covariates specified in a model. In general, this can improve precision when the covariates explain outcome variation and can adjust the comparison for baseline characteristics or measurements. The registry does not identify the covariates, model terms, or exact covariance structure used for the primary analysis, so those details cannot be reconstructed from the posted results.

The primary estimate is -1.773, with a 95% confidence interval from -2.380 to -1.166 and p < 0.001. The treatment difference is reported for the two treatment groups. Interpreting its sign requires attention to the contrast direction: the negative estimate corresponds to lower mean IOP for BOL-303259-X relative to timolol maleate. The posted record does not describe how treatment sequence or period was represented in the ANCOVA, which is relevant to a crossover study.

What does a confidence interval express?

In general, a confidence interval describes the range of estimates compatible with the observed data under a specified statistical procedure and its assumptions. A narrower interval indicates greater precision for the estimated treatment difference, while a wider interval indicates more uncertainty about its magnitude. A confidence interval is not a range containing every participant’s response, and it does not assign a probability to the fixed treatment effect after the data have been observed. The primary interval is entirely below zero, which is consistent with the negative estimated treatment difference under the reported model.

What does the p-value address?

In general, a p-value measures how unusual data at least as inconsistent with a null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The reported p < 0.001 belongs to the sponsor’s ANCOVA result. The p-value of 0.017 belongs to the simple recalculation, which is not the same analysis and should not be substituted for the registry’s reported result.

What is the recalculation based on?

The recalculated primary comparison uses the posted group means, standard deviations, and participant counts to form an approximate, unadjusted comparison. It reports an estimated mean difference of -1.78, an approximate 95% confidence interval from -3.241 to -0.319, and an unadjusted p-value of 0.017. Because it is based on group summaries, it cannot account for participant-level covariates, within-participant correlation, treatment sequence, or other model features unless those are represented in the available summaries. The standard deviations are used as approximate inputs for this calculation. These limits help explain why the recalculated interval and p-value differ from the reported ANCOVA result.

Why does crossover structure matter?

In general, crossover studies can compare treatments within the same participant, using the fact that each participant serves as their own reference. This can reduce the influence of stable differences between participants, but the analysis needs to consider the relationship between repeated measurements and the treatment periods. Treatment sequence, period effects, and possible carryover from one treatment period to another may also matter. The registry identifies the design as crossover, but does not report enough detail to determine how these features were handled in the primary model. It would therefore be inappropriate to assume a particular paired analysis or to treat the reported group summaries as if they were a complete account of the crossover data.

The reported secondary analysis for IOP area under the curve over 24 hours uses ANOVA. In general, ANOVA compares means across groups under a model; the registry labels the reported parameter as mean difference (final values). The record gives a treatment difference of -1.770, a 95% confidence interval from -2.915 to -0.625, and p = 0.004. The model specification and any adjustment terms are not reported. A separate simple recalculation for that endpoint is also based on aggregate group summaries, so it is not a substitute for the registry’s analysis.

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. If present and not accounted for, uncertainty estimates can be too small, making confidence intervals narrower and p-values smaller than warranted. The registry does not report an over-dispersion assessment, so no conclusion about whether it arose in this study can be drawn. More broadly, the registry record does not report the detailed statistical analysis plan, model diagnostics, interim analyses, or missing-data sensitivity analyses.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is -1.773, with a 95% confidence interval from -2.380 to -1.166. The interval describes uncertainty around the estimated treatment difference under the reported ANCOVA analysis. All of its values are negative, so the reported model places the difference in the direction of lower mean IOP for BOL-303259-X relative to timolol. The interval does not describe variation among individual participants and should not be read as a prediction interval for individual outcomes.

The simple recalculation gives a mean difference of -1.78, with an approximate 95% confidence interval from -3.241 to -0.319. That interval is wider than the sponsor’s reported interval and comes from a different method. The recalculation uses only aggregate group summaries and approximations; the sponsor’s ANCOVA uses a model. The reported registry estimate and its confidence interval therefore have priority when describing the sponsor’s primary analysis, while the recalculation illustrates how a simple summary-statistic approach can produce a different precision estimate.

A confidence interval’s width reflects both the amount of information available and the analysis assumptions. The primary endpoint summaries list 21 participants per treatment group. The trial’s crossover structure may provide within-participant information, but the registry does not report the detailed model structure or covariance handling. Without those details, the source of the difference in precision cannot be isolated from the registry record.

Precision is distinct from clinical importance. The interval quantifies statistical uncertainty around the estimated difference; it does not establish whether a difference of a particular size matters to participants. The registry does not report a threshold for clinical importance. Precision is also distinct from generalizability: a relatively precise estimate in this study does not by itself show that the same result would apply in other settings.

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 events. They are illustrations based on the observed effect, not the study’s original design calculations. 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 a stated fraction of the observed effect. The registry’s original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm in the planning illustration for a design with an 80% chance of detecting the specified effect if that effect and the assumptions were correct. The 90% power column gives the corresponding number per arm for a 90% chance. These are design targets under the calculation assumptions, not evidence that the completed trial had either probability of detecting an effect.

The rows scale the assumed effect to 100%, 75%, or 50% of the observed effect. Smaller effects require more participants to distinguish them from random variation under otherwise comparable assumptions. For example, the primary endpoint planning figures are 29 participants per arm for 80% power and 39 for 90% power when planning for 100% of the observed effect; for 50% of the observed effect, they are 116 and 155 per arm, respectively.

This is not observed power. The figures do not report the probability that the completed study detected its result, and they do not show what the original investigators planned. They are conditional planning illustrations based on the observed effect and stated calculation assumptions. Their purpose is to show how the required sample size changes as the target effect and desired power change.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -1.780; pooled standard deviation σ = 2.415.
2. n = 2 × (1.96 + 0.842)² × 2.415² / -1.780² = 28.9, rounded up to 29 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -1.78                      # observed difference in means
sigma <- 2.41541921827247                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1707381)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 29 (80% power), 39 (90% power)
 75% of observed effect: n per arm = 52 (80% power), 69 (90% power)
 50% of observed effect: n per arm = 116 (80% power), 155 (90% power)
power.t.test: 29.9 
Simulated power at n = 29 per arm: 0.786 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s primary reported analysis is ANCOVA: treatment difference -1.773, 95% confidence interval from -2.380 to -1.166, and p < 0.001. The simple recalculation from the posted summary statistics gives a mean difference of -1.78, an approximate 95% confidence interval from -3.241 to -0.319, and an unadjusted p-value of 0.017. The point estimates are similar in direction and magnitude, but the interval and p-value differ.

That difference is expected to be taken seriously rather than treated as a contradiction that can be resolved from the summaries alone. The recalculation uses an approximate, unadjusted method based on group-level means, standard deviations, and counts. It does not reconstruct the sponsor’s model or use participant-level data. The registry identifies the primary reported method as ANCOVA, but does not give the full model specification.

Because the record flags a discrepancy between the recalculated and reported results, the sponsor’s own analysis takes precedence for interpreting the primary inferential result. The recalculated result remains a descriptive check on the posted summaries, not a replacement for the reported analysis. It should not be used to override the confidence interval or p-value from the sponsor’s ANCOVA.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists two secondary outcomes. Multiple outcomes raise a multiplicity question: when several statistical tests are conducted, a result may appear notable by chance even if none of the underlying effects is present. In general, investigators may address this through a prespecified testing order, adjusted significance thresholds, or other methods. The record does not report whether any multiplicity procedure or hierarchy was planned or applied, so the reported p-values should not be assumed to account for testing across outcomes.

The registry does not report interim analyses or stopping rules. It also does not report the full statistical analysis plan or enough model detail to assess all analytic choices. The absence of those details in the record is not evidence that such procedures were or were not used; they are not reported in the registry record.

The primary population is defined as randomized participants who received at least one dose of study drug and had a baseline and at least one postbaseline intraocular pressure assessment. This definition gives a clear minimum set of requirements for inclusion in that analysis. It is not, however, a complete account of how all randomized participants were handled. Enrollment was 25, while the primary outcome summaries list 21 participants per treatment. The reasons for the difference, the number of participants with missing assessments, and the handling of incomplete data are not reported in the registry record.

Missing outcome data can affect both the estimated treatment difference and its precision, particularly if missingness is related to participant characteristics or outcomes. General statistical approaches include complete-case analyses, imputation, or model-based methods, but the record does not say which approach, if any, was used beyond the stated analysis-population definition. No sensitivity analysis addressing missing outcomes is reported.

The crossover design also makes the analysis population and missingness details relevant to interpretation: an incomplete treatment period may affect which within-participant comparisons are available. The registry does not report period-specific participant counts or how incomplete crossover data were incorporated. These limits do not establish that the reported analysis is invalid, but they restrict independent assessment of its assumptions and robustness.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse event summaries list 23 participants at risk in each treatment group. No serious adverse events are reported in either group, and no deaths are reported. The record lists four participants with other adverse events in the timolol maleate group and one in the BOL-303259-X group. These are counts from the posted summaries, not a comparison adjusted for exposure or other factors.

Serious and other adverse events are separate categories in the registry summary. The absence of reported serious events in these groups does not establish that no serious events could occur, and the other-event counts alone do not show that one treatment caused more or fewer events. The registry does not provide event terms in the serious-adverse-event summary, and no serious event terms are listed.

These safety figures should be read in light of the small study and the four-week treatment descriptions. They do not provide a comprehensive estimate of uncommon or longer-term harms. The registry record does not report enough detail about event definitions, severity grading, relatedness assessment, or exposure-adjusted rates to support a broader safety comparison.

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

The posted primary analysis estimates a negative treatment difference for 24-hour IOP, with a 95% confidence interval below zero and p < 0.001. In the direction used for the comparison, the estimated mean IOP is lower under BOL-303259-X than under timolol maleate in this study. The result applies to the defined endpoint, treatment period, study population, and reported model; it is not a statement about every participant’s response.

A statistical result does not by itself establish clinical importance. The registry does not state what size of IOP difference would be considered clinically important, and the confidence interval is not a measure of individual benefit or harm. The outcome is a pressure measure after four weeks of treatment, not a direct assessment of longer-term outcomes or every consequence relevant to participants.

The study compared two active treatments in a randomized, open-label crossover design at a single center. It does not establish how either treatment compares with no treatment or placebo, and it cannot resolve questions that were not measured. The study’s size and setting also limit how broadly its estimates can be applied. The registry record does not report enough detail about treatment sequences, washout, model specification, or missing-data handling to fully assess those aspects of the analysis.

The sponsor’s ANCOVA result is the primary reported inferential analysis. The separate calculation from summary statistics is approximate and unadjusted, and it produces a different confidence interval and p-value. It is useful as a check based on aggregate numbers, but it should not be treated as an alternative primary analysis. The secondary IOP result is directionally consistent with the primary comparison, but multiplicity procedures are not reported and another listed secondary outcome has no posted result.

The appropriate interpretation is therefore bounded: the registry reports a treatment difference in the measured IOP endpoint under its primary model, with quantified statistical uncertainty. The result does not alone establish a universal treatment effect, clinical importance, long-term effects, or a complete safety profile.

18. Why This Trial Matters Statistically

This study illustrates why the design and analysis method matter when interpreting a treatment comparison. A crossover design can make within-participant comparisons possible, but it also requires attention to repeated measurements, treatment sequence, and period effects. The registry identifies the crossover model, yet does not provide enough detail to determine how those features entered the primary analysis. That gap is a practical reminder that a design label alone does not describe the analysis fully.

It also shows the distinction between an adjusted model-based result and a simple recalculation from group summaries. The recalculation gives a useful transparent check, but it cannot recreate participant-level structure or the sponsor’s ANCOVA. Its uncertainty differs from the registry’s reported uncertainty. Where the record flags a discrepancy, the sponsor’s analysis takes precedence, while the recalculation remains an approximate comparison rather than an independent adjudication.

The outcome counts and overall enrollment prompt another statistical question: which participants contributed to each result, and how were incomplete observations handled? The registry defines the primary analysis population, but does not explain the count difference or report missing-data methods. Clear reporting of participant flow and analysis choices is central to judging whether an estimate is robust.

Finally, planning illustrations based on an observed effect should not be confused with the original design rationale or with observed power. Their values depend on assumptions and target effects. Keeping those distinct helps readers understand what the trial’s reported estimates say, what a planning calculation can illustrate, and what remains unknown from the registry record.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information reported for this study. It is a completed, randomized, single-center, open-label phase 2 crossover trial with enrollment of 25. The primary outcome summaries list 21 participants per treatment, but the registry does not explain the difference from total enrollment or provide a participant-flow account. The defined primary analysis population requires dosing and both baseline and postbaseline assessments, so the posted estimate does not necessarily represent every randomized participant.

The treatment descriptions specify four weeks of dosing, but the registry does not report the crossover sequences, period-specific counts, washout interval, or detailed assessment schedule. Those details would help readers assess possible period and carryover effects. The registry also does not report the full ANCOVA specification, including covariates or how the crossover structure was represented. The sponsor’s reported estimate therefore cannot be independently reproduced from the registry summaries alone.

The primary summary-statistic recalculation is approximate and unadjusted. It does not use participant-level data and yields a different confidence interval and p-value from the reported ANCOVA. The registry does not provide enough information to determine which modeling choices account for the difference, so the recalculation should not be treated as a competing definitive analysis.

Only one of the two listed secondary outcomes has a posted analysis. Multiplicity handling, interim analyses, detailed missing-data procedures, and sensitivity analyses are not reported in the registry record. The safety summaries are also limited: they do not provide detailed event definitions, relatedness, or exposure-adjusted comparisons. These reporting limits restrict independent assessment of the results and their broader interpretation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BOL-303259-X With Timolol 0.5% in Subjects With Open-Angle Glaucoma or Ocular Hypertension — NCT01707381.
• Registry record last updated 2018-09-04; status last verified 2018-08.
• Results first posted 2018-09-04.
• 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

NCT01707381 is a completed, randomized, single-center, open-label, phase 2 crossover study comparing BOL-303259-X with timolol maleate ophthalmic solution 0.5% in participants with open-angle glaucoma or ocular hypertension. Enrollment was 25. The treatment descriptions specify once-daily evening dosing for BOL-303259-X and twice-daily dosing for timolol maleate, each for four weeks.

The primary endpoint was 24-hour IOP after four weeks. The registry reports an ANCOVA treatment difference of -1.773, with a 95% confidence interval from -2.380 to -1.166 and p < 0.001. A simple recalculation from posted summary statistics gives a different uncertainty estimate; the sponsor’s reported analysis takes precedence. The record lists two secondary outcomes, but only one has a posted analysis. It reports no serious adverse events or deaths in the summarized groups. Important details about the crossover analysis, missing data, and multiplicity are not reported in the registry record.