Refitting Frequent Replacement Lens Wearers Into Clariti 1 Day And 1-Day Acuvue Moist Daily Disposable Spherical Lenses: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Refitting Frequent Replacement Lens Wearers Into Clariti 1 Day And 1-Day Acuvue Moist Daily Disposable Spherical Lenses (NCT04195893), a randomized na study. The primary outcome is Lens Handling for Lens Insertion.

2. Clinical Question

In practical statistical terms, the record describes a comparison of subjective insertion handling after participants were assigned to wear both lenses in different orders. A crossover design can allow each participant to experience both products, but the validity and interpretation of a crossover comparison depend on how repeated measurements, treatment order, and any period effects are handled. Those details are not reported in the registry record. The posted result therefore describes the recorded group means and their unadjusted comparison, rather than a fully documented crossover analysis.

3. Trial Design

The study is listed as randomized, double-masked, and crossover. Its objective was to evaluate and compare somofilcon A with etafilcon A when worn as daily disposable lenses over approximately one week. The record describes two sequences: somofilcon A followed by etafilcon A, or etafilcon A followed by somofilcon A. Participants were randomized to one of these sequences. Each sequence involved one week of wear with the first lens and then one week with the other lens.

The registry lists enrollment of 56 and a completed status. The recorded study start was 2019-11-24, and primary completion was 2020-02-12. The primary endpoint is a Day 1 subjective rating of lens handling for insertion. The record also lists secondary measures of lens centration, post-blink movement, and push-up tightness. It reports 19 outcome measures, while six secondary results are posted in the available outcome summaries.

Randomization refers to assignment to the order in which the two lenses were worn. Double masking indicates the registry’s masking classification; further details about who was masked or how masking was maintained are not reported in the registry record. The planned approach to sequence allocation, any washout between periods, and the timing of assessments beyond the listed outcome timeframes are not reported in the registry record.

A crossover trial differs from a parallel-group trial because participants can contribute observations under both treatments. In general, an analysis intended to estimate a treatment contrast in a crossover design needs to account for the within-participant relationship and may need to consider period or sequence effects. The posted primary comparison is not described as such an analysis, and the registry reports no analyses. The record does not state how the crossover structure was incorporated into the sponsor’s analysis, if at all.

The record does not report a phase, a sample-size justification, a statistical analysis plan, or the original design assumptions. The planning figures associated with the displayed outcomes are illustrations based on the observed effects, rather than documentation of the study’s original design calculations.

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.

First Intervention

Second Intervention

Reasons for not completing this period:

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 for Lens Insertion, measured over Day 1.

The primary endpoint is mean lens handling for lens insertion on Day 1. Participants rated insertion on an integer scale from 0 to 10, with 0 defined as very difficult and 10 as very easy. The registry reports the result in units on a scale, as a mean and standard deviation for each lens.

This endpoint captures the participant’s subjective experience of inserting the lens. A rating scale makes that experience amenable to quantitative description: the mean gives the average rating in the reported group, while the standard deviation describes how spread out individual ratings were around that average. The scale’s stated anchors help establish what low and high ratings mean, but the registry does not report a threshold for interpreting a difference as important to participants.

The outcome is relevant to the study objective because the stated aim is to compare performance when the lenses are worn in a daily disposable modality. An insertion rating addresses one aspect of lens handling, not every aspect of lens performance. It should not be treated as a direct measure of clinical benefit or as a substitute for the secondary measures of lens position and movement.

The summaries report mean ratings of 9.3 for somofilcon A and 8.0 for etafilcon A, with standard deviations of 1.0 and 1.9, respectively. These are descriptive summaries of the posted Day 1 outcome. The registry does not report additional endpoint details such as a prespecified clinically meaningful difference, a missing-data rule, or an analysis population definition.

7. Results Posted in the Registry

• Etafilcon A: mean 8.00 versus 9.30 on control; difference -1.30 (95% CI -1.87 to -0.73), standardized effect d = -0.86; z-test p = <0.001.

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:
  • Etafilcon A: mean 0.70 versus 0.80 on control; difference -0.10 (95% CI -0.33 to 0.13), standardized effect d = -0.16; z-test p = 0.389.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Etafilcon A 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:
  • Etafilcon A: mean 0.30 versus 0.30 on control; difference 0.00 (95% CI -0.04 to 0.04), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Etafilcon A and the control. The interval gives the range of effects that remain compatible with the data.

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:
  • Etafilcon A: mean 49.00 versus 51.00 on control; difference -2.00 (95% CI -3.87 to -0.13), standardized effect d = -0.40; z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Etafilcon A than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover lens position and movement at baseline after 10 minutes of lens fitting: lens centration, post-blink movement, and push-up tightness. Their overall pattern is not uniform. The displayed summaries include outcomes with little apparent separation between the reported means and an outcome with a mean difference in the same general direction as the primary comparison. The secondary endpoints therefore address distinct aspects of lens fit and should not be expected to reproduce the insertion-handling result exactly.

These measures complement the primary endpoint rather than directly verifying it. Insertion handling is a subjective Day 1 rating, whereas the secondary measures describe fitted-lens characteristics at a specified baseline assessment. A difference in one domain does not necessarily imply a difference in another. The registry does not report a combined outcome or a model linking handling ratings to centration, movement, or tightness.

The secondary comparisons are unadjusted, and the registry lists 19 outcome measures overall while posting six secondary results. In general, examining multiple outcomes increases the chance that some comparisons will look statistically unusual by chance alone. Without a reported multiplicity procedure, analysis plan, or clear hierarchy for interpreting the secondary endpoints, individual unadjusted p-values should carry less weight than a prespecified primary result. They are best treated as descriptive or exploratory evidence, not as independent confirmation of the primary result.

The record does not report the sponsor’s statistical analyses for these secondary measures. The posted results include summary statistics and some unadjusted comparisons, but they do not document the handling of repeated measurements, sequence, or missing observations. A fuller interpretation would require the prespecified role of each endpoint and an analysis that respects the crossover structure.

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: it is a numerical rating summarized by a mean. The registry reports a mean and standard deviation for each lens, followed by a mean difference, confidence interval, and unadjusted p-value. These summaries answer different questions. The means describe the average ratings, the standard deviations describe participant-to-participant spread, the mean difference estimates the contrast, the confidence interval describes its precision, and the p-value measures compatibility with a null comparison under the calculation’s assumptions.

What does the mean difference represent?

The comparison is defined as etafilcon A minus somofilcon A. The reported estimate of -1.3 is therefore the mean for etafilcon A relative to the mean for somofilcon A, not the reverse contrast. A negative value means the first named lens in that subtraction has a lower reported mean. The scale anchors make the direction interpretable: 0 is very difficult and 10 is very easy. The estimate is in rating-scale units and should not be confused with a percentage or a ratio.

The standard deviation is not the uncertainty in the mean difference. It describes the spread of individual ratings within a lens summary. For somofilcon A, the mean was 9.3 and the standard deviation was 1.0; for etafilcon A, the mean was 8.0 and the standard deviation was 1.9. The greater spread in the latter summary indicates more variation around its mean in the posted data. It does not by itself explain why ratings differed or indicate the distribution of individual paired changes.

How should the p-value be read?

The unadjusted p-value is <0.001. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that the result will replicate. The registry does not report the sponsor’s statistical test or a complete statistical analysis plan, so the displayed p-value should be read as an unadjusted comparison, not as a fully documented model-based crossover analysis.

In general, an unadjusted result is calculated without correcting for the number of outcomes or comparisons considered. This matters when many outcomes are examined: the chance of at least one apparently unusual result can rise as the number of tests increases. The registry lists 19 outcome measures and posts six secondary results, but does not report a multiplicity strategy or a formal analysis plan. The primary comparison is also identified by the registry, but any broader family of hypotheses is not documented.

Why does the crossover design matter?

In general, observations from the same participant tend to be related. When a participant wears both lenses, an analysis can use the within-participant contrast rather than treating the two lens summaries as unrelated groups. That can affect the estimated uncertainty and the confidence interval. The posted record contains lens-specific summaries, but does not state whether the primary comparison uses paired participant data or a method that accounts for the randomized sequence.

Period and sequence are also relevant in crossover studies. A period effect is a difference associated with the time or order of measurement rather than the lens itself. A carryover effect refers to an influence of an earlier treatment that persists into a later period. These are general design concepts, not documented findings in this study. Whether either issue was assessed, and whether there was a washout, is not reported in the registry record. The observed numbers alone do not establish that such effects were present or absent.

What does the confidence interval add?

The reported 95% confidence interval runs from -1.867 to -0.733. In general, a confidence interval expresses uncertainty around an estimate under the method used: intervals that are narrower indicate greater precision, while wider intervals indicate more uncertainty. It gives a range of estimates compatible with the data and calculation, rather than a range containing a stated proportion of individual participants’ ratings. It also does not account for design features that were not included in the underlying calculation.

The interval is entirely on the negative side of zero for the stated subtraction, consistent with the direction of the estimated difference. Its limits remain on the 0-to-10 rating scale’s difference scale. The confidence interval does not tell whether the difference is meaningful to participants; the registry does not report a meaningful-difference threshold.

What can be inferred from the posted analysis?

The posted summaries allow a reader to describe the reported group means and the unadjusted mean contrast. They do not provide participant-level data, a detailed model specification, or reported analyses that would establish how the randomized sequence and repeated observations were handled. The record lists no reported analyses. For that reason, the displayed comparison should not be mistaken for a documented sponsor analysis of all crossover features. No discrepancy between a sponsor analysis and the posted comparison is identified in the registry record.

In general, over-dispersion matters when outcome variability is greater than an analysis assumes, because uncertainty may then be understated by a model that does not allow for that extra variation. Here the outcome is a bounded integer scale and the registry reports standard deviations, but no diagnostic assessment, distributional model, or adjustment for the scale’s bounds is reported. The available summaries do not support a claim about whether the analysis assumptions were met.

Finally, the reported comparison does not reveal the distribution of individual changes, the proportion of participants preferring either lens, or how many observations were missing. Those quantities cannot be reconstructed from the means and standard deviations alone. The registry record does not report them.

11. Confidence Intervals and Precision

The primary mean difference is -1.3 rating-scale units for etafilcon A relative to somofilcon A. Its reported 95% confidence interval extends from -1.867 to -0.733. The interval gives a sense of precision around the estimated difference under the calculation used: it spans values that all have the same direction relative to zero. The unadjusted p-value is <0.001.

Precision is not the same as importance. The confidence interval describes uncertainty in the estimated contrast, not the range of ratings among participants and not a threshold for a worthwhile difference. The registry does not report a prespecified meaningful-difference threshold, so the interval cannot determine whether every value it contains would matter in practice.

In general, confidence intervals rely on the statistical method and its assumptions. The registry identifies a crossover design, but does not report whether the comparison accounts for paired observations, treatment order, or period effects. Thus, the displayed interval’s precision should be interpreted in light of the information actually documented: lens-specific means and standard deviations, and an unadjusted comparison. If the analysis does not reflect the crossover structure, its uncertainty may not represent the uncertainty from a suitable crossover analysis.

The summaries report 55 observations for each lens. The record does not say whether all observations came from the same participants, explain the difference from the enrollment of 56, or describe missing-data handling. Such details can affect the population represented and the precision of a treatment contrast. The confidence interval is therefore useful for understanding the posted comparison, but it does not resolve the unreported features of the analysis or establish generalizability beyond the registry’s recorded participants.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. For these continuous outcomes, the figures are participants per arm; the record’s general note says time-to-event planning figures, if present, would instead count total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to a stated fraction of the observed effect.

The 80% power column gives the estimated participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding estimate for a 90% chance. These are design-planning quantities, not statements about the probability that the observed result is true. This is not observed power.

For the primary outcome, the planning row for 100% of the observed effect lists 22 participants per arm for 80% power and 29 for 90% power. The row for 75% lists 39 and 51 participants per arm, and the row for 50% lists 86 and 115. The progression illustrates a general planning principle: smaller effects are harder to detect, so more participants are needed to achieve the same target power.

The primary endpoint was measured in a crossover trial, while these illustrations assume equal allocation between two arms and use a normal approximation. The registry does not report the original sample-size assumptions or explain how the posted planning approach relates to the crossover design. The figures should therefore be read as hypothetical planning guidance based on the observed effect, not as a reconstruction of the trial’s intended sample size or a claim about its design adequacy.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -1.300; pooled standard deviation σ = 1.518.
2. n = 2 × (1.96 + 0.842)² × 1.518² / -1.300² = 21.4, rounded up to 22 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 <- -1.3                      # observed difference in means
sigma <- 1.5182226450689                     # 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(4195893)
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 = 22 (80% power), 29 (90% power)
 75% of observed effect: n per arm = 39 (80% power), 51 (90% power)
 50% of observed effect: n per arm = 86 (80% power), 115 (90% power)
power.t.test: 22.4 
Simulated power at n = 22 per arm: 0.794 (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 record does not report a statistical analysis plan, a multiplicity adjustment, or a hierarchy for testing outcomes. It lists 19 outcome measures and posts six secondary results. The primary endpoint is identified, but the record does not say whether it was the only formally tested primary hypothesis or how the other outcomes were intended to contribute to conclusions.

Multiplicity is the general problem that arises when several statistical comparisons are made. If each test is considered separately without adjustment, the chance of at least one small p-value can be greater across the full set of tests than for a single test. An adjustment or a prespecified testing order can address that issue, but no such approach is reported in the registry record. The secondary p-values should consequently be interpreted cautiously and not as if each were an isolated confirmatory test.

Missing-data rules and the analysis population are also not reported in the registry record. Enrollment is 56, while the primary summaries show 55 participants for each lens. The record does not explain this difference, identify which participants contributed to each outcome, or state how incomplete assessments were handled. It does not report whether analyses followed the randomized sequence assignment, included only participants with measurements under both lenses, or used another population definition.

These gaps matter especially for a crossover study. In general, incomplete observations in one period can change which within-participant comparisons are available. The registry does not report the extent or pattern of missing observations, or whether any method was used to address them. No conclusion about the direction or impact of missing data can be drawn from the posted summaries.

The registry lists no reported analyses. Accordingly, the posted comparisons do not provide enough detail to assess the sponsor’s analysis choices, multiplicity handling, or population definitions. These are documentation limits, not evidence that a particular method was or was not used outside the registry record.

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 4% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events for 55 participants at risk in each lens group. The recorded number affected by serious adverse events is 0 for somofilcon A and 0 for etafilcon A. No deaths are listed in either group, and no serious adverse-event terms are listed.

For other adverse events, 55 participants are listed at risk in each group. The registry records 2 affected in the somofilcon A group and 0 in the etafilcon A group. These counts should be read as the posted safety summaries; the record does not provide event descriptions, severity details for the other events, or an analysis comparing event rates.

The safety summaries do not establish that no adverse events of any kind occurred: they distinguish serious events from other adverse events, and the latter include a recorded count for somofilcon A. They also do not provide enough information to characterize causality, timing, duration, or the experience of individuals. The figures describe the registry record’s reported counts, not a comprehensive assessment of safety.

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

The posted primary result describes a higher mean Day 1 lens-insertion rating for somofilcon A than for etafilcon A. The reported difference, expressed as etafilcon A minus somofilcon A, is -1.3 on the scale from 0, very difficult, to 10, very easy. The 95% confidence interval is from -1.867 to -0.733, and the unadjusted p-value is <0.001. Those statistics indicate a clear separation between the reported means under the posted unadjusted comparison.

That finding does not establish that the difference is practically important. The registry does not report a threshold for a meaningful rating difference, and a statistical result alone cannot determine how participants value a change. Nor does the insertion rating represent all aspects of lens performance. The registry also reports secondary measurements, but the record does not provide a combined assessment that would support an overall ranking of the lenses.

The result also does not establish how a fully specified crossover analysis would compare the lenses. Participants were randomized to different sequences and the study is listed as crossover, but the registry does not report whether the primary comparison accounts for paired observations, sequence, or period. The posted summaries do not reveal individual changes or the extent of missing data. These limits make the result a description of the available registry summaries, rather than a complete causal estimate under a documented statistical plan.

The endpoint is measured on Day 1. It should not be interpreted as evidence about outcomes at later times or beyond the approximately one-week wear periods described in the study objective. The registry record does not report longer-term findings for this endpoint.

In short, the numbers support a descriptive statement about the posted average insertion ratings and their unadjusted comparison. They do not, on their own, establish which lens is preferable overall, the relevance of the difference to individuals, or the performance of either lens in populations beyond those represented by the recorded study.

17. Why This Trial Matters Statistically

This trial is statistically notable because the registry describes a randomized crossover design but posts lens-specific summaries and an unadjusted comparison without reporting an analysis plan. A crossover can generate paired data, and paired information may be handled differently from data in a conventional parallel-group comparison. Readers therefore need to distinguish the design label from the analysis actually documented in the outcome record.

The primary endpoint is a subjective rating on an anchored integer scale. Its mean provides a compact summary, but the standard deviations show that ratings vary among participants. The mean difference and confidence interval add information about the group-level contrast, while leaving unanswered whether the difference is meaningful to participants. That distinction between statistical evidence and practical importance is central to interpreting rating-scale outcomes.

The record also lists multiple outcomes, but reports no multiplicity plan and no analyses. This makes the primary and secondary findings unequal in evidential status: the primary comparison is the designated main outcome, while unadjusted secondary comparisons should be regarded more cautiously. The distinction helps prevent isolated results among several endpoints from being treated as decisive evidence.

Finally, the difference between enrollment and the outcome summaries, together with absent details about missing data and analysis populations, illustrates how registry summaries can be informative yet incomplete. The posted statistics allow a reader to understand the direction and precision of the primary summary comparison. They do not replace a detailed protocol, participant-level analysis, or transparent report of crossover methods.

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.

Several limitations specific to this record constrain interpretation. The registry identifies a crossover design, but does not explain whether or how the primary comparison accounted for repeated observations from the same participants. Sequence and period effects, and any carryover assessment, are not reported in the registry record. The timing or presence of a washout between the one-week lens periods is also not reported.

The registry lists enrollment of 56, while the primary outcome summaries include 55 participants for each lens. It does not explain the difference or state whether the same participants contributed data under both lenses. Missing-data rules, reasons for missing measurements, and analysis population definitions are not reported. These omissions prevent a clear assessment of the completeness and composition of the primary comparison.

The primary outcome is subjective, and the registry gives scale anchors but does not report a threshold for a meaningful difference. Details of masking implementation and whether participants could distinguish the lenses are not reported. The record therefore does not allow evaluation of how expectations or awareness may have influenced ratings.

The registry lists 19 outcome measures and posts six secondary results, but does not report a multiplicity strategy or a complete statistical analysis plan. It also lists no reported analyses. The displayed p-values and intervals do not supply the missing details about model choice or how the crossover design was represented.

Finally, the primary measure is explicitly a Day 1 rating. The registry’s objective refers to approximately one week of wear, but the available primary result does not establish persistence of the rating pattern across that period or beyond it. The record does not report a prespecified practical-importance criterion or enough analysis detail to extend the summary result to broader claims.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Refitting Frequent Replacement Lens Wearers Into Clariti 1 Day And 1-Day Acuvue Moist Daily Disposable Spherical Lenses — NCT04195893.
• Registry record last updated 2020-08-18; status last verified 2020-08.
• Results first posted 2020-08-03.
• 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 BEAGLE 2, a completed randomized, double-masked crossover study of somofilcon A and etafilcon A daily disposable spherical lenses in frequent replacement lens wearers with myopia. Participants were assigned to one of two sequences, with each lens worn for one week.

The primary outcome was a Day 1 subjective lens-insertion handling rating on a scale from 0, very difficult, to 10, very easy. The posted means were 9.3 for somofilcon A and 8.0 for etafilcon A. The unadjusted mean difference, etafilcon A minus somofilcon A, was -1.3, with a 95% confidence interval from -1.867 to -0.733 and p < 0.001.

The registry lists enrollment of 56 and primary summaries of 55 for each lens. It posts secondary outcome summaries, but no reported analyses, statistical analysis plan, multiplicity approach, or missing-data details. The posted comparison is informative as an unadjusted summary, while important details of crossover analysis and interpretation remain unreported in the registry record.