Performance Evaluation of Different Daily Disposable Silicone Hydrogel Contact Lenses: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Performance Evaluation of Different Daily Disposable Silicone Hydrogel Contact Lenses (NCT05805059), a randomized na study. The primary outcome is Lens Handling on Removal.

2. Clinical Question

This is a comparison of two lens products on a subjective handling measure, rather than a comparison of different treatment strategies or a clinical disease outcome. The outcome was collected once on day 6 at the end of wear, according to the registry description. The primary reported contrast is a test-minus-control mean difference of -1.0 units. Its confidence interval extends from -4.869 to 2.869 units, so the posted estimate is compatible with values on either side of no mean difference. The record does not identify additional primary questions or report secondary outcomes.

3. Trial Design

The registry record identifies this as a randomized, double-masked crossover study of the control contact lens (stenfilcon A) and the test contact lens (senofilcon A). It lists the study as completed, with enrollment of 68. The recorded study start was 2023-04-14 and the primary completion date was 2023-06-20. The phase is listed as NA.

The crossover structure used two treatment sequences. One sequence wore the control lens for one week and then crossed over to the test lens for one week. The other sequence wore the test lens for one week and then crossed over to the control lens for one week. Thus, each sequence describes exposure to both products in a different order. The record identifies random allocation and double masking, but does not describe how the sequence allocation was generated or who was masked.

The primary outcome was lens handling on removal, reported as a mean and standard deviation. The registry gives a mean of 95.0 and standard deviation of 12.0 for control, and a mean of 94.0 and standard deviation of 11.0 for test. Each arm listing reports 68. These arm-level summaries alone do not show how outcomes from the two periods were linked within participants, whether the comparison used the crossover structure, or how any sequence or period effects were handled. Those details are not reported in the registry record.

The registry record does not report a washout period, adherence information, a participant flow description, or the number completing each sequence and period. It also does not report the trial's original sample-size justification or a detailed statistical analysis plan. These omissions limit how fully the design and analysis can be reconstructed from the posted 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 (1 Week)

Period 2 (1 Week)

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 on Removal, measured over Collected once on day 6 at the end of wear.

The primary endpoint is “Lens Handling on Removal.” It measures how easy or difficult participants found it to handle the lens when removing it. The outcome uses a 0–100 scale, with 0 defined as very difficult and 100 as very easy. It is reported as a mean with a standard deviation, so the posted summaries describe the average rating and the spread of individual ratings around that average.

The registry record says the measure was collected once on day 6 at the end of wear. A handling rating is relevant to the stated purpose of comparing the performance of two daily disposable silicone hydrogel lenses: it captures a user-perceived aspect of lens use. It is distinct from a measure of visual acuity, ocular health, or a clinical event. The record does not explain how the scale was developed, whether higher scores were considered a particular magnitude of improvement, or what difference participants would regard as important. Consequently, a numerical difference can be described, but its practical importance cannot be established from the posted endpoint description alone.

The reported mean was 95.0 for the control lens and 94.0 for the test lens. The comparison reports a test-minus-control mean difference of -1.0 units. The registry record does not report further details about the instrument's administration, participant-level outcome distributions, or how responses across the crossover periods were combined for analysis.

7. Results Posted in the Registry

• Test Contact Lens: mean 94.00 versus 95.00 on control; difference -1.00 (95% CI -4.87 to 2.87), standardized effect d = -0.09; z-test p = 0.612.

8. Statistical Interpretation

9. Statistical Methods Explained

The endpoint is continuous: each reported score lies on a numerical scale, and the registry summarizes scores using means and standard deviations. A mean describes the center of the observed scores. A standard deviation describes how spread out those scores are around the mean. These summaries are useful for a compact description, but they do not reveal the full shape of the score distribution or whether there were clusters, floor or ceiling effects, or unusual observations.

What does the mean difference describe?

The reported mean difference compares the test lens with the control lens. In the posted comparison, the test mean is 94.0 and the control mean is 95.0, producing a test-minus-control difference of -1.0 units. A mean difference keeps the outcome in its original scale units, which makes it possible to relate the estimate to the 0–100 handling scale. The sign depends on the order of subtraction: negative values indicate a lower test mean than control, while positive values would indicate a higher test mean.

The posted comparison also gives a pooled standard deviation of 11.51. A pooled standard deviation is a combined measure of variability used in some comparisons of two means. A standardized effect expresses a difference relative to a measure of spread, rather than in the original scale units. The comparison's standardized effect is reported as -0.087. That value is a recalculated, unadjusted summary based on the posted means and standard deviations; it should not be taken as a reported model estimate from the trial analysis. The registry record reports no trial analysis models or participant-level results with which to verify a crossover-specific standardized effect.

What does the p-value say?

The unadjusted p-value is 0.612. In general, a p-value describes how compatible the observed data, or more extreme data, are with a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. Interpretation depends on the statistical model and analysis choices. The registry record does not report the trial's own significance threshold or a detailed primary analysis plan. The significance level of 0.05 stated for the planning illustrations applies to those calculations, not necessarily to the trial's analysis.

The p-value is labelled unadjusted. The record does not state that it was adjusted for multiple testing, and the registry lists no posted secondary outcomes. With only the primary outcome described, the record does not establish whether additional analyses were planned or performed outside the posted results. A p-value should therefore be read alongside the estimated difference and its interval, rather than as a stand-alone verdict.

Why does the crossover design matter?

In a crossover trial, participants receive treatments in sequence, so measurements under different treatments can be related within a participant. In general, accounting for that relationship can improve precision compared with treating all observations as independent, but the appropriate analysis depends on the design and data. Period effects, sequence effects, carryover, and missing measurements can also matter in crossover analyses. These are general statistical considerations, not claims about what occurred in this study. The registry record does not report whether a washout was used, how period or sequence effects were considered, or whether the primary comparison used a paired or other crossover model.

The arm summaries list 68 for each lens, but those summaries do not reveal whether all measurements came from complete pairs or how missing period-specific measurements were handled. The recalculated, unadjusted comparison uses the posted summary statistics and should not be confused with a reconstruction of the original crossover analysis. No trial analysis is listed in the registry record.

How should the interval be read?

The confidence interval for the mean difference ranges from -4.869 to 2.869 units. In general, a confidence interval expresses uncertainty around an estimate under the assumptions of the method used to construct it. It identifies values that are reasonably compatible with the data and model, rather than proving that the true effect lies at any particular point. Because this interval includes zero and extends in both directions, the posted results do not determine whether the mean difference favors the control or test lens. The registry record does not state the confidence level or the method used for the original interval, so no further inference about those choices is warranted.

Statistical significance and practical importance are separate questions. A small p-value does not establish importance, and a result that does not cross a conventional threshold does not prove that two products are equivalent. Establishing equivalence would require a prespecified margin and an analysis designed to assess whether the uncertainty stays within that margin. Neither is reported in the registry record.

10. Confidence Intervals and Precision

The mean-difference estimate is -1.0 units, with a confidence interval from -4.869 to 2.869 units. The interval is important because it shows the range of differences compatible with the estimate under the interval's statistical assumptions. It spans zero and includes both negative and positive values. As a result, the posted data do not pin down the direction of the mean difference with precision.

The width of an interval reflects both the amount of information in the data and the variability of the outcome, together with the analysis method. The reported standard deviations are 12.0 for control and 11.0 for test, and the means are close to one another. The interval gives a more direct account of uncertainty in the contrast than either standard deviation does. It should not be interpreted as a range containing most individual participant scores; it concerns the estimated mean difference.

The crossover structure matters when judging precision. Measurements from the same participant may be correlated, and a suitable analysis can use that relationship. However, the registry record does not report the model or method used to construct the interval, nor does it provide participant-level paired data. The interval therefore cannot be independently checked as a crossover-specific estimate from the record alone. The confidence level is also not reported.

The interval does not establish equivalence. That conclusion would require a prespecified range of differences considered unimportant and an appropriate analysis against that range. No such margin is reported. The interval is best read as showing that uncertainty remains around a small estimated mean difference, rather than as evidence that the two lenses have identical handling ratings or that a meaningful difference is impossible.

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 estimates are expressed as participants per arm, not as total events. They are illustrations based on the observed effect and are not the trial's original sample-size justification. The assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect as the effect to detect.

The 80% power column gives the estimated participants per arm for a design that would have an 80% chance of detecting the assumed effect under those planning assumptions, if the effect and model assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities under the assumed effect and statistical model, not guarantees about the result of a future study. They do not say how likely the observed study result was to be significant, and they are not observed power.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller assumed effect is harder to distinguish from random variation, so it requires more participants per arm to reach the same planned power. The estimates increase as the assumed fraction becomes smaller. The original design assumptions, including the effect size used to plan the actual trial, are not reported in the registry record. These figures should therefore be read as conditional illustrations rather than as a description of how enrollment was chosen.

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 = -1.000; pooled standard deviation σ = 11.511.
2. n = 2 × (1.96 + 0.842)² × 11.511² / -1.000² = 2,080.0, rounded up to 2,080 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                      # observed difference in means
sigma <- 11.5108644332213                     # 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(5805059)
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 = 2,080 (80% power), 2,785 (90% power)
 75% of observed effect: n per arm = 3,698 (80% power), 4,951 (90% power)
 50% of observed effect: n per arm = 8,320 (80% power), 11,138 (90% power)
power.t.test: 2080.9 
Simulated power at n = 2,080 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.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when an analysis tests more than one outcome, comparison, time point, or subgroup. When many tests are conducted, the chance of obtaining at least one apparently unusual result can increase. Statistical approaches can account for that risk, but the appropriate choice depends on the questions specified in advance and the analysis plan. The registry record lists one outcome measure and no posted secondary outcomes. It does not report whether other outcomes, time points, or subgroup analyses were planned, or whether any multiplicity adjustment was used.

The primary comparison is accompanied by an unadjusted p-value of 0.612. “Unadjusted” indicates that the posted p-value is not presented as corrected for multiplicity. The record does not provide an analysis plan that would clarify whether adjustment was considered necessary or whether the primary outcome was designated as the sole confirmatory test. It would therefore be inappropriate to infer either that multiplicity was a concern in the trial or that it was fully addressed.

Missing-data handling is also not reported in the registry record. The arm summaries list 68 for control and 68 for test, but those figures do not establish whether every enrolled participant posted a usable outcome in both periods. The record does not describe missing measurements, exclusions, imputation, or sensitivity analyses. These details matter in crossover studies because a participant may have a measurement in one period but not another, affecting which paired comparisons can be made.

The analysis population is not described. The registry record does not state whether the primary outcome used all randomized participants, only participants who completed both periods, or another defined group. Nor does it report a participant flow or a model for repeated measurements. As a result, the posted summaries give a comparison but do not fully document the population and procedures behind it. A fuller statistical interpretation would require the prespecified analysis plan and sufficient participant-level information to understand missingness and the handling of the crossover design.

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 68 participants at risk in each lens group, with zero serious events reported in each. Deaths are listed as zero for each group. The other adverse event figures list 68 at risk in each group and one other event in each group. These are the reported counts for the respective lens groups; they should not be combined into a new total.

These figures are a limited description of events recorded in the registry. The record does not provide event descriptions, severity details for the other events, timing, attribution, or a detailed safety analysis. It also does not explain how event collection was conducted during the crossover periods or how participants with exposure to both lenses were represented in the group figures. The number of events alone cannot establish whether an event was caused by a lens.

Zero reported serious events or deaths in these group listings does not demonstrate that serious events are impossible, and the one other event in each group does not establish a difference between products. Safety conclusions require consideration of the definitions, follow-up, event ascertainment, and the full clinical context, much of which is not reported in the registry record.

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

The result describes the average lens-handling ratings reported for the control and test lenses in this randomized, double-masked crossover study. The control mean was 95.0 and the test mean was 94.0 on a scale from 0 (very difficult) to 100 (very easy). The test-minus-control mean difference was -1.0 units. The interval from -4.869 to 2.869 includes zero, and the unadjusted p-value is 0.612. These findings indicate uncertainty around a small estimated mean difference; they do not establish a clear direction of difference.

The result does not establish that the lenses are equivalent. Equivalence requires a clinically justified margin set in advance and an analysis designed to assess whether the data exclude differences beyond that margin. The registry record does not report such a margin or analysis. Nor does the result establish that either lens is better or worse overall. It addresses the posted primary handling measure, not every aspect of lens performance or every possible outcome.

The study design is a crossover, but the analysis model and participant-level results are not reported. Therefore, the posted summaries do not show how the within-participant relationship, sequence, or period was handled. That limits conclusions about the precision and interpretation of the comparison. The outcome is also a participant-reported handling rating, and the registry record does not describe a threshold for a meaningful difference or the scale's measurement properties.

The safety listings report no serious adverse events or deaths in either group and one other adverse event in each. Those counts are descriptive and limited; they do not establish comparative safety. Overall, the posted data support a narrow statement about the observed means, interval, and reported events. They do not settle broader questions about clinical benefit, overall performance, equivalence, or safety.

16. Why This Trial Matters Statistically

This study is statistically interesting because it uses a crossover design to compare two products on a continuous, participant-rated outcome. Crossover designs can make within-participant comparisons possible: each participant may contribute information under both products. In general, such designs can be informative when the outcome is measured comparably across periods and when the analysis accounts for the structure of the data. The registry record reports the treatment sequences but does not describe the primary analysis model, making the connection between design and analysis an important point for interpretation.

The observed means are close, and the estimated difference is small in the original scale units. Yet the interval spans zero and extends in both directions. This is a useful illustration of why a point estimate alone is not enough: the interval communicates uncertainty about the direction and magnitude of the contrast. Conversely, a p-value alone does not explain how large an effect might be or whether that size would matter to participants.

The example also distinguishes a failure to establish a difference from evidence of equivalence. A result with an interval including zero does not demonstrate that two products perform the same. A formal equivalence question requires an explicit margin and a suitable design and analysis. Neither is reported in the registry record.

Finally, the planning illustrations show how sample-size requirements depend on the effect one aims to detect. Smaller target effects require more participants per arm under the stated assumptions. Because the record does not report the original design assumptions, these calculations are useful as conditional planning examples, not as an explanation of the actual enrollment decision. Together, the result highlights the importance of prespecified analysis methods, crossover-aware reporting, and a clear definition of what difference would be meaningful.

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 registry record leaves several trial-specific details unavailable. Although it reports random allocation and double masking, it does not describe the randomization procedure, the parties masked, or how masking was maintained. It gives two treatment sequences, but does not report whether there was a washout period between lens periods. Without those details, the possibility of period, sequence, or carryover influences cannot be assessed from the posted record.

The primary outcome is described as a rating collected once on day 6 at the end of wear. The record does not describe the scale's validation, instructions to participants, administration procedures, or threshold for a meaningful difference. The outcome is a subjective handling measure, so interpretation is limited to that reported experience and should not be extended to other performance or clinical outcomes.

The registry record does not report participant characteristics beyond the condition of myopia, nor does it provide a flow of participants through the sequences and periods. It lists 68 for each lens summary, but does not state the number with complete paired outcomes or explain missing-data handling. The primary analysis model is not described, so it is unknown from the record whether the comparison accounted for within-participant correlation or period and sequence effects.

No secondary outcomes or analyses are posted, and the original sample-size assumptions and analysis plan are not reported. The reported confidence interval's level and construction method are also not identified. These omissions do not change the numerical summaries, but they constrain independent assessment of the analysis and the scope of conclusions that can be drawn.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Performance Evaluation of Different Daily Disposable Silicone Hydrogel Contact Lenses — NCT05805059.
• Registry record last updated 2024-09-26; status last verified 2023-03.
• Results first posted 2024-09-26.
• 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

The registry record describes a completed randomized, double-masked crossover study comparing control contact lenses (stenfilcon A) with test contact lenses (senofilcon A) in participants with myopia. Enrollment is listed as 68. The two sequences each involved one week with one lens followed by one week with the other.

The primary outcome was lens handling on removal, rated on a 0–100 scale from very difficult to very easy and collected once on day 6 at the end of wear. The reported means were 95.0 for control and 94.0 for test. The test-minus-control mean difference was -1.0, with a confidence interval from -4.869 to 2.869 and an unadjusted p-value of 0.612.

The adverse event listings report zero serious events and zero deaths in each group, and one other event in each group. No secondary outcomes or trial analyses are posted. The crossover-specific analysis method, missing-data approach, analysis population, and original sample-size justification are not reported in the registry record.