Comparing The Performance Of Two Different Daily Disposable Lenses (MIKI): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing The Performance Of Two Different Daily Disposable Lenses (MIKI) (NCT04492397), a randomized na study. The primary outcome is Overall Lens Fit Acceptance.

2. Clinical Question

This question concerns a measured fit rating, not a broad assessment of every aspect of lens performance. The primary outcome is a score on a scale from 0 to 4, recorded in 0.50 steps. The scale description ranges from a lens that should not be worn at all to a perfect fit. The registry’s stated objective was to compare the performance of the two lenses over approximately one week each. It does not report additional details about the participants’ baseline characteristics, the criteria used to select them, or the intended interpretation of a small difference in this rating. Those omissions limit how far the result can be generalized or translated into a practical threshold.

3. Trial Design

The registry describes a randomized, double-masked, crossover study with an enrollment of 35. Each participant was assigned to one of two sequences: test lens followed by control lens, or control lens followed by test lens. Each lens period lasted one week. Thus, participants were intended to experience both lenses, with the order determined by randomization. This is different from a parallel-group design in which each participant receives only one of the two interventions.

A crossover design can allow comparisons within the same participant, which may account for stable differences between people. To use that feature appropriately, an analysis generally needs information about each participant’s paired measurements and may need to consider period or sequence effects. The registry record does not describe whether or how such features were handled. It also does not report a washout period, the masking procedures, who was masked, or the details of lens fitting and assessment.

The study status is completed. The registry lists a start date of 2020-09-30 and a primary completion date of 2021-03-31. The phase is recorded as NA. CooperVision, Inc. is listed as the sponsor. The registry describes the interventions as test and control contact lens devices and gives the intended one-week sequence for each group.

Although the trial is crossover, the displayed arm summaries report 35 observations for each lens. The posted comparison is a simple unadjusted recalculation from the summary statistics, rather than a reported participant-level crossover analysis. The registry record reports no analyses. It does not explain the original statistical design, its sample-size justification, its planned treatment of the paired data, or any interim analysis. Those details 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.

Before assignment: Forty-one subjects were screened and 35 subjects started and completed the study.

First Intervention

Second Intervention

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: Forty-one subjects were screened and demographic data includes all screened subjects.

6. Primary Endpoint

The registry lists the primary outcome as Overall Lens Fit Acceptance, measured over 1 week.

The primary endpoint is overall lens fit acceptance, measured in units on a scale after one week. The registry describes a rating from 0 to 4 in 0.50 steps. Its anchors distinguish a lens that should not be worn at all, a borderline but unacceptable fit, a minimally acceptable fit, a fit that is not perfect but is acceptable to dispense, and a perfect fit. The posted endpoint is summarized as a mean and standard deviation for each lens.

A fit-acceptance rating is used to condense an assessment of how acceptable the overall fit is into a single measure that can be compared between lenses. A mean provides a summary of the group’s ratings, while the standard deviation describes variation among those ratings. Because the scale has ordered descriptive categories and half-step increments, the mean is a compact summary; it does not show the full distribution of responses or how many participants selected each rating.

The registry’s objective makes this rating the central comparison for the study. However, the registry does not report a threshold that would define a meaningful difference, nor does it describe whether a particular score was required for a lens to be considered acceptable. Therefore, the endpoint can be interpreted as a comparative rating, but the clinical meaning of a small difference is not established by the record.

7. Results Posted in the Registry

• Test Contact Lens: mean 3.71 versus 3.73 on control; difference -0.02 (95% CI -0.18 to 0.14), standardized effect d = -0.06; z-test p = 0.806.

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.

Lens Centration

• 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:
  • Test Contact Lens: mean 0.40 versus 0.29 on control; difference 0.11 (95% CI -0.13 to 0.35), standardized effect d = 0.22; z-test p = 0.367.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Contact Lens and the control. The interval gives the range of effects that remain compatible with the data.

Post-blink Movement

• 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:
  • Test Contact Lens: mean 0.20 versus 0.23 on control; difference -0.03 (95% CI -0.06 to -0.00), standardized effect d = -0.50; z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Test Contact Lens than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Push-up Tightness

• 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:
  • Test Contact Lens: mean 51.00 versus 49.00 on control; difference 2.00 (95% CI -0.59 to 4.59), standardized effect d = 0.36; z-test p = 0.130.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Contact Lens and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add measures of lens position, movement after blinking, and tightness assessed by a push-up test. They are distinct from the primary rating of overall fit acceptance. Across these measures, the estimated directions are not uniform: some estimates are higher for the test lens and another is lower. Their confidence intervals and unadjusted p-values also differ in how much uncertainty they express. This variation cautions against treating the secondary outcomes as a single consistent pattern of evidence.

One unadjusted secondary comparison has a confidence interval that excludes zero and an unadjusted p-value below 0.05. The other posted secondary comparisons have intervals that include zero. These results are not substitutes for the primary comparison, which concerns overall lens fit acceptance. Nor does an isolated secondary result establish that a broader performance difference exists. Each outcome measures a different feature, and the registry does not report a prespecified hierarchy or a procedure for drawing a combined conclusion across them.

There are multiple secondary measures, and the registry record does not report adjustment for multiple comparisons. When many outcomes are examined, the chance of at least one apparently unusual result can increase, even if no underlying differences exist. General statistical practice therefore gives unadjusted secondary findings less weight than a prespecified primary analysis, particularly when the analysis plan and multiplicity strategy are not reported.

The secondary measures may help describe aspects of lens behavior, but the record does not explain how they were intended to support or qualify the primary endpoint. Their timing is listed as baseline, and no further timing or interpretation details are reported. The secondary findings should be considered descriptive and exploratory in relation to the primary result, not as independent confirmation or proof of a general difference between lenses.

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

• Lens Centration
• Lens Centration
• Post-blink Movement
• Post-blink Movement
• Push-up Tightness
• Push-up Tightness

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous in the registry’s statistical classification and is reported as a mean with a standard deviation. A mean summarizes the average score in a group. A standard deviation describes how spread out individual scores are around that mean. These summaries are useful for a concise comparison, but they do not reveal the full shape of the score distribution or the number of participants at each response category.

What does the mean difference represent?

The posted primary comparison is the test-lens mean minus the control-lens mean. It is -0.02 units on the acceptance scale. A negative value indicates that the test-lens average is lower than the control-lens average in this contrast; it does not, by itself, say whether the difference matters in practice. The means are 3.71 and 3.73, respectively. Because the scale has a defined upper endpoint of 4, interpretation also depends on the bounded scale and the distribution of individual ratings, neither of which is fully represented by the mean difference alone.

What does the confidence interval add?

A confidence interval describes a range of estimates compatible with the observed data under the calculation’s assumptions. The interval for the primary contrast is -0.179 to 0.139. It includes zero, which represents no difference in means, and extends in both directions. The interval is more informative than the point estimate alone because it conveys uncertainty around that estimate. It does not assign a probability to a particular fixed treatment difference, and it does not determine whether any value in the interval is clinically important.

How should the p-value be read?

The unadjusted p-value for the primary comparison is 0.806. In general, a p-value measures how unusual data at least as incompatible with a null model would be if that model and the calculation’s assumptions held. It is not a measure of effect size, and it is not the probability that a treatment effect is absent. The registry does not report a prespecified decision threshold or a sponsor-reported statistical analysis, so the p-value should be considered alongside the effect estimate, interval, design, and incomplete analysis information.

Why does the crossover design matter?

In a crossover study, each participant receives both interventions in a specified sequence. A paired comparison can account for the fact that two measurements from the same participant are related. In general, a paired analysis uses the within-participant differences and their variability. The amount of variability in those differences depends on the relationship between a participant’s measurements under the two conditions. Separate means and standard deviations do not provide that relationship. The registry record does not report participant-level paired data or the methods used to analyze them.

The posted comparison is a simple unadjusted recalculation from the summary statistics. It should therefore be distinguished from a reported analysis that might model the crossover structure, period, or sequence. The registry reports no analyses, and it does not describe an analysis plan. The record also does not state whether missing outcome data occurred or how missing observations would have been handled. It is not possible to determine from the registry whether all relevant crossover considerations were addressed in an analysis outside the posted record.

What do standard errors and dispersion tell us?

The standard deviations for the primary outcome are 0.33 for the test lens and 0.35 for the control lens. They describe participant-to-participant spread in the posted groups. Standard errors, when reported, describe uncertainty in an estimated mean rather than the spread of individual observations. The registry’s posted primary summaries include standard errors of 0.056 and 0.059 for the test and control means, respectively. These quantities serve different purposes: standard deviations describe variation among ratings, while standard errors describe the precision of estimated means under a calculation’s assumptions.

For a crossover design, general statistical practice would pay attention to the pairing of observations, because treating the two lens periods as unrelated groups may discard information or misstate uncertainty. The summary-statistic recalculation does not recover the within-person association. No adjustment or model for period, sequence, or carryover is described in the registry record, so none should be assumed.

Why do the planning illustrations use assumptions?

The sample-size figures are planning illustrations based on the observed effect and stated assumptions, not the trial’s own original design calculation. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. These assumptions define a hypothetical planning calculation. They do not establish that the original crossover trial was designed using the same method, and the record does not report the original sample-size justification.

General statistical reasoning also distinguishes a planning calculation from the analysis of completed data. Power is a property of a design and a specified effect under assumptions; it is not a retrospective measure of whether a completed study “had enough” information to detect its actual result. The planning figures should be read as illustrations of how a hypothetical study might be sized under their stated assumptions, rather than as evidence about the probability that the observed result is correct.

Finally, statistical significance and practical importance are separate questions. A small p-value does not by itself establish a meaningful difference, while a larger p-value does not prove that there is no difference. The registry does not state a meaningful-difference threshold for acceptance or a planned margin for equivalence. The estimate, interval, study design, and limits of the available analysis information are therefore central to interpretation.

11. Confidence Intervals and Precision

The primary estimate is a test-minus-control mean difference of -0.02, with a confidence interval from -0.179 to 0.139. The interval crosses zero, so the data are compatible with the test lens having a lower mean, the control lens having a lower mean, or the means being very similar. Its range is important: the point estimate alone may look close to zero, but the interval shows that uncertainty remains around the size and direction of the difference.

Precision is not the same as whether a result is statistically significant or practically important. The unadjusted p-value is 0.806, but that value does not establish equality. Conversely, the interval does not say that every value inside it is equally likely or clinically meaningful. The registry record does not provide a threshold for a meaningful change in acceptance, so the clinical interpretation of the interval’s endpoints cannot be determined from the record.

The reported standard deviations are 0.33 for the test lens and 0.35 for the control lens. Those values summarize variation among participant ratings. The means and standard deviations do not show the full response distribution. Nor do separate arm summaries show the within-person correlation expected to be relevant in a crossover study. Because the registry does not report a paired analysis or participant-level data, the precision of a crossover-specific estimate cannot be assessed from the posted summaries.

The confidence interval should therefore be read as the uncertainty accompanying the unadjusted summary-statistic comparison, not as a complete description of uncertainty under every possible analysis of the crossover trial. Greater precision would require more complete information about the analysis and the paired observations.

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 calculated using the observed effect as a starting point and then considering planning for 100%, 75%, and 50% of that observed effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. These are planning assumptions for the illustration; the trial’s original design assumptions and sample-size justification are not reported in the registry record. The illustration also uses a two-arm framing rather than a reported crossover-specific calculation.

For the primary endpoint, planning for 100% of the observed effect gives 4,541 participants per arm for 80% power and 6,079 participants per arm for 90% power. Planning for 75% of the observed effect gives 8,073 participants per arm for 80% power and 10,807 participants per arm for 90% power. Planning for 50% of the observed effect gives 18,163 participants per arm for 80% power and 24,315 participants per arm for 90% power.

In general, the 80% and 90% power columns describe the sample sizes that the stated assumptions would require to have the corresponding chance of detecting the specified effect if that effect and the assumptions were true. The higher power target requires a larger planned sample. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. This is not observed power; it is a hypothetical planning calculation, not a measure of what the completed trial achieved.

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 = -0.020; pooled standard deviation σ = 0.340.
2. n = 2 × (1.96 + 0.842)² × 0.340² / -0.020² = 4,540.6, rounded up to 4,541 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 <- -0.02                      # observed difference in means
sigma <- 0.340147027033899                     # 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(4492397)
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 = 4,541 (80% power), 6,079 (90% power)
 75% of observed effect: n per arm = 8,073 (80% power), 10,807 (90% power)
 50% of observed effect: n per arm = 18,163 (80% power), 24,315 (90% power)
power.t.test: 4541.5 
Simulated power at n = 4,541 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes, including lens centration, post-blink movement, and push-up tightness, with duplicate outcome labels in the record. It reports no analyses for those outcomes and does not describe a statistical plan for controlling the chance of false-positive findings when multiple outcomes are considered. The posted secondary p-values are unadjusted. Without a reported multiplicity strategy, a secondary result should not be treated as though it were the sole prespecified test.

The registry record also does not report whether the primary analysis was designated as the only confirmatory test, whether the secondary outcomes were exploratory, or whether any hierarchy among outcomes was planned. The primary endpoint is identified, but the details of hypothesis testing and interpretation are not. This makes it difficult to know how the results were intended to be weighed together.

Missing-data information is not reported in the registry record. It does not state whether any outcome measurements were missing, how incomplete one-week periods would be handled, or whether all randomized participants were included in the analysis. The number of participants reported for each lens outcome is 35, but the record does not provide participant-level completion information or describe a missing-data method.

The analysis population is also not reported in the registry record. There is no stated intention-to-treat, per-protocol, or other analysis population, and no account of exclusions after randomization. In a crossover study, the handling of participants who do not complete both periods can affect which paired comparisons are available. The record does not explain whether that issue arose or how it would be addressed.

Finally, the registry reports no analyses and does not provide a statistical analysis plan, interim-analysis information, or the sponsor’s analysis methods. These omissions do not prove that such procedures were absent from the study; they mean that their details are not reported in the registry record. They limit assessment of prespecification, missing-data handling, crossover-specific analysis, and the strength of secondary evidence.

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 0% reporting threshold.

The adverse-event figures list 35 participants at risk in each lens group. In each group, the registry reports zero serious adverse events, zero other adverse events, and zero deaths. No serious-event terms are listed. These are the counts recorded in the registry for the reported groups.

Zero reported events means that none were recorded in these categories in the registry data; it does not establish that an event could not occur or that the lenses have no safety risks. The record does not give event definitions, surveillance procedures, exposure time for the adverse-event counts, or details about how events were attributed to a lens. Because the study is crossover, the registry’s group presentation should not be interpreted as two unrelated populations without further information.

The registry also does not report a detailed safety analysis or additional context about withdrawals and adverse events. The counts should therefore be read as a concise description of the posted event categories, not as a comprehensive safety assessment or as medical advice.

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

The primary result is a small estimated difference in mean overall fit acceptance between the test and control lenses: -0.02 units for the test-minus-control contrast. The confidence interval ranges from -0.179 to 0.139, and the unadjusted p-value is 0.806. In general statistical terms, the estimate is close to zero and the interval includes zero, but the result does not prove that the lenses are identical.

The registry does not report a threshold for a difference that would be considered meaningful, nor does it specify an equivalence or noninferiority margin. Without such a threshold, the result cannot establish that any difference within the interval is unimportant. A formal equivalence conclusion requires a prespecified margin and an analysis designed to assess that question; neither is reported in the registry record.

The endpoint is a short-term fit-acceptance rating after one week. It is not a direct measure of every aspect of lens performance, and the registry does not describe longer-term use or other outcomes beyond those listed. The average score does not reveal how individual participants rated the lenses or whether particular subgroups had different experiences. The findings therefore apply to the recorded outcome and study period, rather than supporting broad claims beyond them.

The crossover design means participants were assigned to experience both lenses in a randomized order. The posted comparison is an unadjusted recalculation from summary statistics, and the registry reports no analyses. It does not provide participant-level paired results or the methods needed to evaluate period, sequence, or other crossover considerations. That limits how completely the displayed comparison represents the design.

In sum, the posted data describe similar group mean ratings, with uncertainty around the difference and incomplete information about the analysis. They do not prove equality, establish a meaningful advantage for either lens, or provide a complete account of all aspects of performance. The interpretation should remain tied to the measured outcome, the one-week periods, and the limits of the registry record.

17. Why This Trial Matters Statistically

This trial is statistically notable because its randomized crossover design and its posted comparison summaries do not give the same level of detail. In a crossover, measurements from the same participant can be compared directly, and that pairing may be important for estimating uncertainty. The registry provides separate means and standard deviations and a simple unadjusted comparison, but no participant-level paired results or reported analysis. Readers should therefore distinguish the design’s potential for within-participant comparison from the analysis information actually available in the registry.

The primary estimate is close to zero, but its confidence interval still includes values on either side of zero. This illustrates why a point estimate and a p-value alone are not enough to judge what the data can rule out. A confidence interval helps show the range of estimates compatible with the calculation, while the absence of a meaningful-difference threshold leaves the practical importance unresolved.

The secondary outcomes also illustrate the need to distinguish a primary question from a collection of additional measures. One unadjusted secondary comparison has an interval excluding zero, while the other posted comparisons do not. Without a reported plan for multiple comparisons, an isolated secondary finding deserves cautious interpretation rather than being treated as decisive evidence.

The sample-size illustrations are another useful distinction: they are hypothetical planning calculations under stated assumptions, not the original study rationale and not a retrospective measure of the completed study’s power. The registry does not report the original sample-size justification. Together, these points show why design, analysis, precision, and prespecification all matter when interpreting a clinical trial record.

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 registry record has limited information about the participants beyond the condition of myopia and the enrollment of 35. Further demographic and clinical characteristics are not reported in the registry record. That restricts assessment of how representative the participants may be of other people who use contact lenses.

The primary outcome is a subjective acceptance rating on a bounded scale. The registry provides the scale anchors and group summaries, but not the distribution of individual scores or details about who made the rating and under what assessment conditions. It also does not state what size of difference would be considered meaningful.

The crossover design is not accompanied by a reported participant-level paired analysis. The record does not describe period or sequence effects, carryover, washout, or how incomplete participation across the two lens periods would be handled. These details matter for assessing whether the comparison used the structure of the design appropriately, but they are not reported in the registry record.

The registry lists several secondary measures and reports unadjusted comparisons, without a stated multiplicity approach or a reported statistical analysis plan. It also reports no analyses. Missing-data handling, analysis populations, and the original sample-size justification are not reported in the registry record. The planning illustrations use their own stated assumptions and should not be mistaken for the trial’s original design rationale.

Finally, the reported primary endpoint covers one week of wear per lens. The record does not provide longer-term outcomes or enough detail to extend the comparison beyond the measured outcomes and timeframe. These limitations constrain interpretation of both the estimated difference and the broader relevance of the findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparing The Performance Of Two Different Daily Disposable Lenses (MIKI) — NCT04492397.
• Registry record last updated 2021-06-23; status last verified 2021-06.
• Results first posted 2021-06-21.
• 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 describes a completed randomized, double-masked crossover study of test and control daily disposable contact lenses in participants with myopia. Enrollment was 35; participants were randomized to wear the lenses in opposite one-week sequences. The listed primary outcome was overall lens fit acceptance after one week, measured on a scale from 0 to 4 in 0.50 steps.

The posted mean acceptance scores were 3.71 for the test lens and 3.73 for the control lens. The unadjusted test-minus-control difference was -0.02, with a confidence interval from -0.179 to 0.139 and an unadjusted p-value of 0.806. Secondary measures and adverse-event counts are also recorded. The registry reports no analyses and does not describe the original statistical plan, crossover-specific analysis, missing-data handling, or analysis populations.