Comparing a Monthly Replacement Lens Versus a Daily Disposable Lens: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing a Monthly Replacement Lens Versus a Daily Disposable Lens (NCT06046209), a randomized na study. The primary outcome is Lens Handling at Insertion.

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, crossover study. The registry lists enrollment of 30 participants and describes two sequences: Control Lens followed by Test Lens, and Test Lens followed by Control Lens. In either sequence, participants wore each lens for 90 minutes. The design therefore allows each participant to experience both lens conditions, with the order randomized according to the assigned sequence.

The primary endpoint was assessed immediately after lens application. The registry lists 30 participants for each lens condition, but these condition-specific counts should not be interpreted as 60 different participants: the study is identified as a crossover, and the sequence descriptions indicate that participants wore both lenses. The registry record does not report how many participants were assigned to each sequence, whether all enrolled participants completed both periods, or whether any participants were excluded from the endpoint results.

The registry identifies the study as completed and gives the study start and primary completion dates as 2023-09-28 and 2023-11-22. The phase is listed as NA. The sponsor is CooperVision, Inc. No further details on the masking procedure, randomization method, washout or transition between lenses, or conduct of the study visits are reported in the registry record.

The reported comparison concerns subjective handling ratings, not a clinical outcome or a measure of longer-term lens use. Its interpretation depends on the crossover structure and on how the ratings from the same participants were analyzed. No analysis is posted in the registry record, so the reported summary-statistic comparison does not establish whether the trial’s crossover structure was incorporated in a sponsor analysis.

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: First Intervention-90 Minutes

Period 2: Second Intervention-90 Minutes

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 Lens Handling at Insertion, measured over Immediately after lens application.

The primary endpoint was “Lens Handling at Insertion.” Participants rated the ease of applying each study lens to the eye immediately after lens application. Ratings used an integer scale from 0 to 100, where 100 represented very easy and 0 represented very difficult. The registry reports the endpoint as a mean with standard deviation.

A subjective rating is used to capture the wearer’s immediate experience of handling a lens. It can describe a practical aspect of lens use that is not captured by a clinical examination alone. In this study, the rating was specific to ease of application at insertion; it should not be treated as a measure of comfort, vision, safety, or longer-term preference, none of which is identified as the primary endpoint.

The posted mean was 83.0 for the Control Lens, with a standard deviation of 16.0, and 93.0 for the Test Lens, with a standard deviation of 9.0. These are group summaries of subjective scores. A mean describes the average rating, while the standard deviation describes how spread out ratings were around that average. The endpoint description does not report individual ratings or how many participants selected each possible score.

7. Results Posted in the Registry

• Test Lens: mean 93.00 versus 83.00 on control; difference 10.00 (95% CI 3.43 to 16.57), standardized effect d = 0.77; z-test p = 0.003.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary measure is continuous: each participant gave a score on a 0-to-100 integer scale, and the registry reports means and standard deviations for the two lens conditions. A mean gives the average score within a condition. A standard deviation describes dispersion: larger values indicate more variability among observed scores around the mean. These summaries retain the scale’s direction, where higher ratings mean easier application.

The mean difference compares the average rating for the Test Lens with the average rating for the Control Lens. The recalculated estimate is 10.0 points. Its sign reflects the ordering of the comparison: the Test Lens mean is higher. The reported interval, from 3.431 to 16.57, expresses uncertainty around that estimated mean difference under the unadjusted calculation. A confidence interval is a range generated by a statistical procedure that reflects both the estimate and its sampling uncertainty. It is not a range containing a fixed proportion of individual participants’ scores, and it is not a guarantee that the true difference lies within the particular interval.

The reported p-value is unadjusted and is 0.003. In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The registry record does not report a sponsor analysis or a full statistical analysis plan, so the unadjusted p-value should not be treated as evidence that every feature of the study design was incorporated in the calculation.

The crossover design is a central method issue. In a crossover study, the same participant receives each condition, and the comparison can account for the fact that measurements from one person may resemble each other more than measurements from different people. A paired analysis uses the within-person differences. Its uncertainty depends on the variability of those paired differences, which in turn depends on the relationship between a participant’s ratings under the two conditions. Marginal means and standard deviations alone do not provide that relationship. The posted recalculation uses the summary statistics and is not a substitute for an analysis based on participant-level paired data.

Sequence and period can also matter in crossover designs. The registry describes both orders, with each lens worn for 90 minutes. Randomized order helps distribute order assignment, but interpretation may also depend on carryover, changes over time, and whether the response differs by period or sequence. No washout details, period-specific results, carryover assessment, sequence analysis, or model specification are reported in the registry record. It is therefore not possible to assess from the posted results how those features were handled.

The pooled standard deviation is reported as 12.98, and the standardized difference as 0.770. In general, a pooled standard deviation combines variability estimates from conditions to put a mean difference on a scale relative to observed spread. A standardized effect can help describe magnitude across measurement scales, but it removes the direct interpretation in score points and does not answer whether participants would regard the difference as meaningful. The registry does not report a prespecified threshold for clinical or practical importance.

The result is described as unadjusted. Adjustment can refer to accounting for design features or other variables in a model; the record does not report which covariates, if any, were planned for adjustment. The registry lists zero analyses, so no model-based sponsor result, adjusted estimate, or analysis population definition is available in the registry record. No missing-data method is reported either. General statistical interpretation should therefore distinguish the posted summaries and recalculation from any protocol-specified analysis that may or may not have been conducted.

Finally, statistical evidence and design adequacy are separate questions. A small p-value does not resolve the limitations of a summary-only comparison, and the confidence interval does not address unreported design details. The soundest statistical reading keeps the scale-based descriptive result, the uncertainty interval, the unadjusted nature of the recalculation, and the crossover structure in view together.

10. Confidence Intervals and Precision

The unadjusted mean difference is 10.0 points, and its reported 95% confidence interval extends from 3.431 to 16.57. The interval gives a range of values compatible with the observed data under the calculation used. Its width reflects uncertainty in the estimated contrast, rather than variation among individual ratings. The individual ratings may vary substantially even when the estimated mean difference is relatively precise.

The interval does not incorporate every uncertainty that could matter for this study. In particular, the posted calculation is an unadjusted recalculation from summary statistics, while the trial used a crossover design. The registry record does not provide paired differences, participant-level observations, or an analysis that accounts for within-participant correlation. Without that information, the precision of a crossover-adjusted estimate cannot be assessed from the registry record.

Each condition has 30 observations listed, with standard deviations of 16.0 for the Control Lens and 9.0 for the Test Lens. The registry’s overall enrollment is 30, consistent with a crossover in which participants experience both conditions. The two condition counts therefore do not indicate two separate groups of 30 independent participants. The distinction matters because the dependence between a person’s two ratings affects the standard error and confidence interval for a paired contrast.

The interval quantifies sampling uncertainty under its calculation; it does not address systematic issues such as unreported missing ratings, order or period effects, or how participants were selected. The registry record does not report those details. The interval should consequently be read as precision for the posted unadjusted comparison, not as a complete measure of uncertainty for every possible analysis of the crossover trial.

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 illustrations give participants per arm, not total events. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect used for each planning scenario is a stated fraction of the observed effect. These figures are planning illustrations based on the observed result, not the trial’s original design assumptions; those original assumptions are not reported in the registry record. This is not observed power.

For a planning scenario using 100% of the observed effect, the illustration gives 27 participants per arm for 80% power and 36 participants per arm for 90% power. For 75% of the observed effect, it gives 48 participants per arm for 80% power and 63 participants per arm for 90% power. For 50% of the observed effect, it gives 106 participants per arm for 80% power and 142 participants per arm for 90% power.

In plain terms, the 80% column gives the planned number per arm for a design with an 80% chance of detecting the stated effect under the listed assumptions. The 90% column gives the number per arm for a higher planned chance of detection, with the other assumptions held as specified. Smaller effects need more participants because they are harder to distinguish from ordinary sampling variation. These calculations use a two-arm framework and should not be treated as a reconstruction of the crossover trial’s design, since the registry record does not report its original sample-size justification or assumptions.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 10.000; pooled standard deviation σ = 12.981.
2. n = 2 × (1.96 + 0.842)² × 12.981² / 10.000² = 26.5, rounded up to 27 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 <- 10                      # observed difference in means
sigma <- 12.9807549857472                     # 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(6046209)
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 = 27 (80% power), 36 (90% power)
 75% of observed effect: n per arm = 48 (80% power), 63 (90% power)
 50% of observed effect: n per arm = 106 (80% power), 142 (90% power)
power.t.test: 27.4 
Simulated power at n = 27 per arm: 0.797 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and no posted secondary outcomes. It also lists zero analyses. The record therefore does not show a set of sponsor-reported hypothesis tests from which to determine whether adjustments for multiple comparisons were applied. A multiplicity plan, including any rules for handling more than one endpoint, time point, or analysis, is not reported in the registry record.

Multiplicity is a general statistical concern when many hypotheses are tested: the chance of at least one apparently unusual result can increase as the number of tests increases. Whether an adjustment is needed depends on the planned family of analyses and the inferential goals. Because the registry does not report a statistical analysis plan or a collection of posted analysis results, it is not possible to determine which comparisons were prespecified, whether additional analyses were performed, or how the unadjusted p-value fits into any broader testing strategy.

The registry record does not report missing-data counts, reasons for missingness, or a method for handling missing ratings. The enrollment is 30, and 30 participants are listed for each lens condition, but those condition counts do not establish that every participant had complete paired outcome data or that no values were excluded. The record also does not describe an intention-to-treat or per-protocol population, or another analysis population definition. Those details are not reported in the registry record.

These omissions matter because missing observations and population definitions can affect both the estimate and its uncertainty, especially in a crossover where an incomplete participant record may leave one condition without its paired rating. The registry record also does not say whether missingness was assessed by sequence or period. No conclusion about the effect of missing data or multiplicity can be drawn from the posted summaries alone.

The unadjusted recalculation should therefore be understood as a statistical comparison of the posted summaries, not as confirmation of the trial’s complete prespecified analysis strategy. The analysis plan, multiplicity handling, missing-data approach, and analysis populations are not reported in the registry record.

14. 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.

The registry lists 0 serious adverse events among 30 participants for the Control Lens and 0 among 30 for the Test Lens. It also lists 0 other adverse events among 30 in each condition and 0 deaths in each condition. No serious adverse event terms are listed.

These are the posted counts, not evidence that an event was impossible or that no unreported event occurred. The registry record does not provide event-level descriptions, timing, severity beyond the serious-event classification, or a detailed account of how safety events were collected. The condition-specific denominators occur in a crossover study, so they should not be interpreted as 60 unique participants.

The posted safety figures are distinct from the primary handling endpoint, which measured subjective ease of application. The registry record does not report a broader safety analysis or additional safety outcomes. The zero counts describe what was recorded in the registry for these categories and this study; they do not establish safety beyond the scope of the recorded information.

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

The posted results show higher mean immediate ease-of-application ratings for the Test Lens than for the Control Lens: 93.0 compared with 83.0. The unadjusted mean difference is 10.0 points, with a 95% confidence interval from 3.431 to 16.57 and an unadjusted p-value of 0.003. On the rating scale, higher values represent easier application, so the observed direction favors the Test Lens rating for this specific task.

This result is about subjective ratings immediately after application. It does not establish a difference in comfort, vision, ocular health, continued use, preference over time, or any other outcome not reported as the primary endpoint. The registry record does not report a threshold that defines a practically meaningful score difference, so statistical evidence for a difference should not be equated with a claim about how important the difference is to wearers.

The comparison also needs to be read in light of the crossover design. Participants wore both lenses, and the registry describes randomized order. The posted recalculation is unadjusted and based on summary statistics; the record does not report a sponsor analysis that accounts for the paired measurements. The unadjusted interval and p-value therefore do not provide a complete account of the statistical analysis appropriate to the crossover structure.

The trial enrolled 30 participants, and the registry lists 30 observations for each lens condition. Its results should not be generalized beyond the population and setting described without further evidence. The record does not report participant characteristics beyond habitual soft lens wearers and myopia, nor does it report subgroup or longer-term results. These boundaries do not negate the posted descriptive comparison; they clarify that it addresses a narrow, immediate, self-reported handling outcome.

In short, the posted data describe a higher average handling score for the Test Lens condition, with an unadjusted uncertainty interval that excludes zero. They do not by themselves establish broader clinical benefit, participant-level importance, or the result of a crossover-adjusted sponsor analysis.

16. Why This Trial Matters Statistically

This trial is statistically interesting because its design and its posted comparison do not line up in the simplest way. A crossover design measures each participant under both lens conditions, allowing a within-person comparison. That design can be useful for subjective outcomes because each participant can serve as their own comparator. But exploiting that feature requires an analysis that preserves the pairing, and the registry record does not post such an analysis.

The distinction between independent-group and paired uncertainty is important. Marginal means and standard deviations describe each condition separately, while a paired comparison also depends on how strongly each participant’s two scores are related. That within-person relationship is not available in the posted summaries. Consequently, the unadjusted recalculation is informative as a summary-based comparison but cannot show how the uncertainty would change in an analysis using the paired observations.

The endpoint also illustrates the difference between statistical evidence and practical interpretation. A scale-based mean difference and confidence interval convey a direction and uncertainty in score points. A p-value addresses compatibility with a null hypothesis under a test’s assumptions. Neither statistic alone identifies what amount of change matters to participants. The registry does not report a meaningful-difference threshold, so interpretation should stay anchored to the measured task and scale.

Finally, the record gives a compact result but leaves important analysis details unreported: the trial’s original sample-size assumptions, the paired-data analysis, missing-data handling, and analysis populations. Recognizing these boundaries is part of interpreting trial results rigorously. It prevents a descriptive difference from being mistaken for a full account of the study’s design-based inference.

17. Limitations

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

The primary limitation for statistical interpretation is that the trial is a crossover, but the posted comparison is an unadjusted recalculation from summary statistics. The record does not provide individual paired ratings, paired differences, or a sponsor analysis that accounts for the relationship between the two scores from each participant. Therefore, the confidence interval and p-value should not be assumed to represent a crossover-adjusted analysis.

The registry record does not report allocation counts by sequence, period-specific results, a washout or transition procedure, or an assessment of order, period, or carryover effects. It also does not describe the randomization method or masking procedure. These missing design details limit assessment of how the crossover was implemented and analyzed.

Further limitations are that the record does not report participant characteristics beyond habitual soft lens wearers and myopia, a threshold for a meaningful score difference, missing-data counts or methods, or a definition of the analysis population. No secondary results are posted, and the registry lists no analyses. The trial’s original sample-size justification and statistical analysis plan are not reported in the registry record.

The endpoint is an immediate subjective ease-of-application rating. Results cannot be extended from that measure alone to longer-term use or other clinical outcomes. The enrollment was 30, and the registry’s condition-specific counts are not separate groups of unique participants in this crossover study. These limits apply to interpretation of the posted record and do not establish whether unreported analyses or details exist elsewhere.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Comparing a Monthly Replacement Lens Versus a Daily Disposable Lens — NCT06046209.
• Registry record last updated 2024-12-12; status last verified 2024-01.
• Results first posted 2024-12-12.
• 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.

21. Record Summary

NCT06046209 is a completed, randomized, double-masked crossover study sponsored by CooperVision, Inc. It enrolled 30 participants and compared a Control Lens with a Test Lens in habitual soft lens wearers with myopia. Participants wore each lens for 90 minutes, in randomized order.

The primary outcome was an immediate subjective rating of ease of lens application on a 0-to-100 scale. The mean was 83.0 for the Control Lens and 93.0 for the Test Lens. The unadjusted mean difference was 10.0, with a 95% confidence interval from 3.431 to 16.57 and an unadjusted p-value of 0.003. No analyses or secondary outcomes are posted. Safety listings report 0 serious adverse events, 0 other adverse events, and 0 deaths for each lens condition.

The registry record does not report the sponsor’s crossover analysis, missing-data methods, or original sample-size assumptions.