The Comparative Clinical Performance of Two Daily Disposable Toric Contact Lenses: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Comparative Clinical Performance of Two Daily Disposable Toric Contact Lenses (NCT05020990), a randomized na study. The primary outcome is Subjective Handling Rating on Lens Removal.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, crossover trial comparing two daily disposable toric contact lenses. The registry record identifies the study as completed and gives an enrollment of 55. It lists astigmatism as the condition and CooperVision, Inc. as the sponsor. The trial is marked as not applicable for phase.

In a crossover design, participants receive both study conditions in sequence rather than remaining in only one condition throughout the study. The record describes two sequences: Lens A followed by Lens B, and Lens B followed by Lens A. Each lens was worn for one week within its sequence. Random allocation to sequence can help distribute order effects, but the method used to generate the allocation sequence and the allocation concealment procedures are not reported in the registry record.

The record identifies masking as single, but does not specify which people were masked or how masking was maintained. It does not report whether participants could distinguish the lenses, whether outcome assessors were masked, or what procedures were used to limit expectation effects. A washout interval between lenses is not reported in the registry record. Nor is an explanation of whether such an interval was considered necessary.

The trial began on 2022-04-01 and had a primary completion date of 2022-09-30. The primary endpoint was assessed at one week. These registry entries describe the registered design and schedule; they do not by themselves establish how closely conduct matched the plan. Protocol details, deviations beyond those described in the outcome population note, and the original statistical design assumptions are not reported in the registry record.

Because participants experienced both lenses, observations from the same person may be related. A crossover analysis can account for that within-person relationship and, depending on its specification, sequence or period effects. The registry record does not report an analysis of those features. The posted means and comparison should therefore be read with attention to the fact that the design was crossover, while the registry does not describe a paired or period-adjusted 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.

Before assignment: Five participants were initially ineligible, but were re-enrolled following a protocol amendment that expanded the age range and allowed the use of an increased range of lens axes for Lens A.

Period 1 (One Week)

Period 2 (One Week)

Analysis population for the primary outcome, as defined in the registry: Lens A: all data for one participant was discounted, as the follow-up visit took place significantly outside the date range for this visit. Lens B: all data for a different participant was discounted, as the follow-up visit took place significantly outside the date range for this visit. Another participant's subjective scores and symptoms were not collected at the correct study visit in error, and their data was subsequently excluded from analysis.

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 Subjective Handling Rating on Lens Removal, measured over One week.

The primary endpoint was the subjective handling rating on lens removal after one week. It is a continuous measure on a scale of 0 to 100: 0 means unmanageable removal and 100 means excellent removal. The reported summaries are means and standard deviations, so the outcome is described by its average rating and the variability of individual ratings around that average.

This measure addresses a practical aspect of lens use: how participants perceive removal of the lens. A rating scale can capture subjective experience that may not be represented by a clinical examination alone. At the same time, the score is a report of perceived handling, not a direct measure of visual performance, lens fit, or a broader health outcome. The registry lists overall lens fit and biomicroscopy score at follow-up as secondary outcomes, but the registry entries do not include their results.

The scale endpoints provide meaning to the direction of the score: higher ratings correspond to more favorable removal ratings as defined by the scale. Lens A had a reported mean of 85.5, and Lens B had a reported mean of 83.3. The observed difference in those group means was -2.2 for Lens B relative to Lens A. The registry record does not report a threshold for what participants or investigators would consider an important difference, or a minimally important change. Thus, the scale and mean difference describe the ratings, but do not independently establish the practical importance of the contrast.

7. Results Posted in the Registry

• Lens B: mean 83.30 versus 85.50 on control; difference -2.20 (95% CI -9.45 to 5.05), standardized effect d = -0.12; z-test p = 0.552.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean and standard deviation describe?

For a continuous outcome such as a rating scale, the mean is the arithmetic average of the recorded values. It summarizes the center of the observations but does not show the full distribution. The standard deviation describes how spread out the individual values are around that mean. It is not the uncertainty interval for the mean and it does not show whether every participant rated the lenses similarly.

Lens A had a mean rating of 85.5 and standard deviation of 17.7 among 53 observations. Lens B had a mean of 83.3 and standard deviation of 20.1 among 52 observations. The standard deviations indicate that ratings varied across observations. Means alone can conceal that variation, so the spread matters when interpreting how representative an average may be for individual ratings.

How should the mean difference be read?

The comparison is expressed as Lens B relative to Lens A. The estimated difference was -2.2 units. A negative sign indicates that the Lens B mean was lower than the Lens A mean in the posted summaries. The difference is measured on the original scale, which makes it possible to relate the estimate to the scale's defined endpoints. The record does not state how large a difference would be meaningful to participants or investigators.

A mean difference is an estimate, not a known fixed contrast. Its uncertainty depends on the observed data and the statistical model used. The posted confidence interval for the comparison runs from -9.449 to 5.049. Because this interval includes zero, it does not distinguish a difference in one direction from no difference or a difference in the other direction at the conventional level associated with that interval. The interval should be considered alongside the point estimate rather than replaced by a yes-or-no reading of the p-value.

What does the p-value convey?

The unadjusted p-value was 0.552. In general, a p-value is calculated under a statistical model that specifies a null hypothesis, commonly no difference, and measures how unusual the observed result would be if that model held. It is not the probability that the null hypothesis is true, nor is it the probability that the observed result happened by chance. A larger p-value does not demonstrate equivalence, and it does not quantify the size or importance of a difference.

The reported p-value is unadjusted. The registry does not report a multiplicity correction or a full statistical analysis plan, so the p-value should not be interpreted as if a particular family of outcomes or tests had been accounted for. The analysis population and model specifications are also not described in detail.

Why does the crossover design matter?

In a crossover study, each participant receives both conditions, so a participant's observations under the two lenses may be correlated. A paired analysis uses the within-participant contrast and can account for that correlation. In general, positive within-participant correlation can make paired comparisons more precise than an analysis that treats observations from the same participant as unrelated. The amount and direction of the correlation in this trial are not reported.

Period and sequence can also matter in crossover studies. Ratings may differ between the first and second wearing periods, and the order in which lenses are used may be relevant. Carryover from one condition to the next is another design consideration. The registry does not report whether these effects were assessed, how they would be handled, or whether a washout period occurred. It is therefore not possible to infer the crossover model from the design description alone.

The comparison figures are unadjusted re-calculations from posted summary statistics rather than a reported paired crossover analysis. The registry record lists zero analyses. It does not describe an alternative sponsor analysis in sufficient detail to identify a model that accounts for the crossover structure. Accordingly, the comparison is informative as a contrast of the posted group summaries, but its precision should not be mistaken for a documented within-participant analysis.

What do standardized effects and planning illustrations add?

The standardized difference was -0.116. In general, a standardized effect expresses a mean contrast relative to a measure of outcome variability. This can help compare scales with different units, but interpretation depends on the variability measure and context. It does not provide a participant-centered threshold for importance and should not displace the original-scale difference.

The sample-size display uses planning illustrations based on fractions of the observed effect. Such illustrations can help show how the size of a target effect relates to a required sample size under stated assumptions. They do not describe the trial's original design justification, which is not reported in the registry record. They also do not turn the observed estimate into a reliable target effect: an estimate from a small or imprecise study may itself be uncertain.

In general, over-dispersion means that observed variability is greater than assumed by a statistical model, which can make model-based uncertainty too small if it is not accommodated. The registry summaries report standard deviations but do not identify a model for over-dispersion or a model-based adjustment. For this continuous outcome, the reported spread is useful descriptive information, but there is not enough detail to state whether a specific variance assumption was tested.

10. Confidence Intervals and Precision

The confidence interval for the mean difference, Lens B relative to Lens A, extends from -9.449 to 5.049. It gives a range of values compatible with the observed data under the calculation's assumptions. The estimate at the center of the comparison is -2.2, but the interval includes values below and above zero. This means the reported data do not pin down the direction of the difference with high precision.

A confidence interval is not a range containing a fixed proportion of individual participant ratings. It describes uncertainty about an estimated quantity, here the mean difference. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. Its interpretation depends on the statistical method and assumptions used. In this trial, the posted comparison is an unadjusted summary-statistic calculation, and the registry does not report a paired crossover analysis. The interval therefore should not be read as evidence that within-participant correlation, sequence, or period effects have been modeled.

The point estimate is small relative to the scale's full span, but the record does not report a threshold for a meaningful difference. It is not appropriate to label the interval as clinically unimportant simply because it crosses zero or because the point estimate is -2.2. The interval also leaves open the possibility of a difference in either direction. Without a prespecified equivalence or noninferiority margin, it cannot establish that the lenses perform equivalently within an acceptable range.

The standard deviations, 17.7 for Lens A and 20.1 for Lens B, describe variability in the observed ratings; they do not resolve uncertainty about the crossover contrast. The within-participant correlation and the details of missing-data handling are not reported, limiting assessment of the precision of a paired comparison.

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 sample-size table and curve are planning illustrations based on the observed effect, not the trial's original design calculation. The displayed figures are participants per arm, not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which the assumed effect would be detected with 80% power, given those planning assumptions. The 90% power column gives the corresponding number per arm for 90% power. In general, power is the probability that a specified statistical test will reject its null hypothesis under a particular assumed effect and model. These columns compare planning scenarios; they do not describe what happened in the completed trial.

The displayed scenarios use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The figures for 80% power are 1,162, 2,066, and 4,648 participants per arm, respectively. The corresponding 90% power figures are 1,556, 2,766, and 6,222 participants per arm. Smaller assumed effects need more participants to detect under the stated assumptions, which is why the figures increase as the assumed fraction of the observed effect decreases.

This is not observed power. It is a forward-looking planning illustration that applies assumed effect sizes and model conditions to the posted estimate. Since the observed effect itself is uncertain, these figures should not be treated as a definitive design recommendation or as evidence that the completed study was adequately or inadequately powered.

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 = -2.200; pooled standard deviation σ = 18.926.
2. n = 2 × (1.96 + 0.842)² × 18.926² / -2.200² = 1,161.8, rounded up to 1,162 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 <- -2.2                      # observed difference in means
sigma <- 18.9264262778393                     # 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(5020990)
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 = 1,162 (80% power), 1,556 (90% power)
 75% of observed effect: n per arm = 2,066 (80% power), 2,766 (90% power)
 50% of observed effect: n per arm = 4,648 (80% power), 6,222 (90% power)
power.t.test: 1162.8 
Simulated power at n = 1,162 per arm: 0.800 (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, subjective handling rating on lens removal, and two secondary outcomes: overall lens fit at follow-up and biomicroscopy score at follow-up. It also records three outcome measures and zero analyses. Results for the two secondary outcomes are not reported in the registry record. The number of statistical tests actually performed and the relationship between the listed outcome measures and analyses are therefore not described.

When several outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. In general, multiplicity procedures may adjust the interpretation of p-values or confidence intervals to account for a defined family of tests. Whether such adjustment is needed depends on the prespecified questions and analysis plan. A multiplicity strategy is not reported in the registry record, so the unadjusted p-value for the primary comparison should not be presented as a multiplicity-adjusted result.

The primary outcome population note says all data for one participant were discounted for Lens A because the follow-up visit took place significantly outside the date range for that visit. For Lens B, the note says all data for a different participant were discounted for the same stated reason, then begins an additional statement that is incomplete. The full detail of that additional statement is not reported in the registry record. The reported primary summaries use 53 observations for Lens A and 52 for Lens B.

Other missing-data details are not reported in the registry record. This includes whether missingness occurred for reasons beyond the visit-date issue, how any other missing observations were handled, and whether imputation or sensitivity analyses were performed. The record does not describe a prespecified analysis population, a formal intention-to-treat approach, or a per-protocol population. It is therefore not possible to determine from the registry entries how the analysis population was defined beyond the stated discounted data.

The record also does not report the complete statistical analysis plan, the handling of crossover period or sequence, or whether the primary analysis used within-participant data. These omissions limit evaluation of multiplicity, missing-data assumptions, and the precise inferential method. They do not change the numerical summaries, but they constrain the conclusions that can be drawn from them.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list 54 participants at risk for each lens. Serious adverse events affected 0 participants for Lens A and 0 for Lens B. Deaths were 0 in both groups. The registry lists no serious adverse event terms among its top reported terms.

These figures describe the reported serious-event counts within the registry's safety summaries. They should not be read as proof that no safety events of any kind occurred. The record separately lists other adverse events affecting 5 participants for Lens A and 1 for Lens B. The record does not provide further detail in the registry record about the nature, severity, timing, or relationship of those other events.

The trial was a crossover study, but the safety summary is grouped by lens. The registry entries do not explain how participants were attributed to safety groups, how exposure periods were handled, or whether participants could contribute to both lens summaries. No event rates or comparative safety estimates are reported, and no statistical safety analysis is described. These counts should therefore be interpreted as descriptive registry entries, not as a definitive comparison of safety between lenses.

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

The posted primary outcome describes participants' subjective ratings of removal after one week of wearing each lens. The mean was 85.5 for Lens A and 83.3 for Lens B, with a reported mean difference of -2.2 for Lens B relative to Lens A. The confidence interval, from -9.449 to 5.049, includes zero and allows differences in either direction. The unadjusted p-value was 0.552.

These statistics do not establish that the lenses are identical or equivalent. A nonsignificant p-value is not a test of equivalence, and the registry does not report an equivalence margin, a noninferiority margin, or an analysis designed to support either conclusion. Nor does the result establish that any possible difference is important or unimportant to participants, because a threshold for meaningful change is not reported.

The outcome is one subjective rating on a defined scale. It should not be generalized to other aspects of lens performance or to the secondary outcomes, whose results are not reported. The trial record concerns participants with astigmatism and these two lens products in the described one-week crossover sequences. The registry entries do not establish how the result applies to people, settings, or use patterns outside that study description.

Interpretation is also limited by the lack of a reported paired crossover analysis and incomplete information on the analysis population and missing data. The reported summary comparison does not document how within-participant correlation, sequence, or period effects were handled. The registry's observation that some follow-up data were discounted because visits were outside the specified date range further matters when considering which observations contributed to the means.

The most direct statistical conclusion is descriptive: the posted group means were 85.5 and 83.3, and the estimated mean difference was -2.2 with an interval spanning zero. The uncertainty and missing analysis details mean that a stronger claim about a reliable directional difference, equivalence, or broader performance is not supported by the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why study design and analysis need to be read together. A crossover design exposes participants to both lenses and can support a within-person comparison. That feature can be valuable for a subjective rating because each participant's experience under one lens may be compared with their experience under the other. But the benefit depends on analysis that appropriately uses the paired observations and considers relevant features such as period and sequence. Those details are not reported in the registry record.

The posted comparison gives a clear estimate on the original rating scale: -2.2 units for Lens B relative to Lens A. Its confidence interval extends from -9.449 to 5.049, so the point estimate should not be mistaken for a precise account of the difference. The interval captures uncertainty under the reported calculation, while the missing crossover analysis information leaves open whether a different model would yield different uncertainty.

The outcome also demonstrates the distinction between statistical and practical interpretation. A rating scale has defined endpoints, but the registry does not identify a threshold for a meaningful difference. A p-value of 0.552 does not show equivalence, and a confidence interval crossing zero does not show that all practically relevant differences have been ruled out. The result must be interpreted in the context of the question and the precision of the estimate.

Finally, the population note makes data handling relevant to interpretation. The record describes discounting follow-up data for participants because visits fell outside the specified date range, while the Lens B note is incomplete. The registry entries do not describe additional missing-data methods or the analysis population in full. These limitations show why reporting the outcome summaries alongside complete analysis methods is important for evaluating a randomized crossover trial.

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.

Several limitations specific to this trial affect interpretation. First, the registry describes a crossover design but does not report a paired analysis or explain whether the posted comparison accounts for within-participant correlation. The analysis of period, sequence, or possible carryover effects is also not reported. The confidence interval and p-value should therefore be understood as belonging to the posted unadjusted summary-statistic comparison, not as a documented full crossover model.

Second, the primary outcome population note identifies discounted data for one participant for Lens A and a different participant for Lens B because their follow-up visits took place significantly outside the visit date range. The Lens B note then begins another exclusion statement but is incomplete. Its full text and any additional implications for the analysis population are not reported in the registry record. Other missing-data handling, including any imputation or sensitivity analysis, is not reported.

Third, although the registry lists overall lens fit and biomicroscopy score as secondary outcomes, their results are not included in the registry record. The number and handling of all analyses are not described; the record lists zero analyses. A multiplicity plan is not reported, and the unadjusted primary comparison should not be treated as if it accounted for other outcomes or tests.

Fourth, no threshold for a meaningful rating difference, equivalence margin, or noninferiority margin is reported. That prevents interpretation of the estimate as establishing practical similarity or an acceptable difference. The registry also does not provide the original sample-size justification or the trial's own design assumptions.

Finally, details about the masking procedures, allocation method, any washout period, adherence, and the identities of people masked are not reported in the registry record. These missing design and analysis details limit assessment of potential bias and the strength of conclusions that can be drawn from the numerical summaries.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: The Comparative Clinical Performance of Two Daily Disposable Toric Contact Lenses — NCT05020990.
• Registry record last updated 2023-12-20; status last verified 2023-09.
• Results first posted 2023-12-20.
• 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

NCT05020990 is a completed, randomized, single-masked crossover trial titled “The Comparative Clinical Performance of Two Daily Disposable Toric Contact Lenses,” sponsored by CooperVision, Inc. It enrolled 55 participants and lists astigmatism as the condition. The study compared Lens A (delefilcon A) with Lens B (stenfilcon A), using sequences in which each lens was worn for one week.

The primary outcome was subjective handling rating on lens removal at one week, measured on a 0-to-100 scale. The reported means were 85.5 for Lens A and 83.3 for Lens B. The Lens B relative-to-Lens A mean difference was -2.2, with a confidence interval from -9.449 to 5.049 and an unadjusted p-value of 0.552.

The record lists overall lens fit and biomicroscopy score as secondary outcomes but does not report their results in the registry record. It reports no serious adverse events affecting participants in either lens group and 0 deaths in both groups. Details of the paired crossover analysis, full missing-data handling, and original design assumptions are not reported in the registry record.