Ocular Characteristics in Contact Lens and Spectacle Wear: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ocular Characteristics in Contact Lens and Spectacle Wear (NCT03913377), a randomized na study. The primary outcome is Non-Invasive Break Up Time (NIBUT) or Non-Invasive Keratograph Break Up Time (NIKBUT).

2. Clinical Question

This is a question about a measured ocular characteristic under two optical-correction conditions, not a direct assessment of all aspects of visual experience or eye health. The posted primary outcome is a continuous measure expressed in seconds, summarized as a mean and standard deviation. The randomized sequence assignment supports a planned within-participant crossover comparison, while the posted summary statistics also allow a simple unadjusted comparison of the reported condition means. Those approaches do not necessarily use the same information or yield the same estimate.

3. Trial Design

The registry record describes a randomized, open-label, 2-treatment by 2-period crossover study, with a 1-week washout between study periods intended to reduce potential carryover. Participants in the interventional arm were habitual contact lens wearers who owned spectacles. They were randomized to one of two sequences: spectacle wear followed by ACUVUE OASYS 1-Day, or ACUVUE OASYS 1-Day followed by spectacle wear. The registry describes no masking.

The study also included an observational arm of eligible habitual spectacle wearers. Those participants used their habitual optical correction and underwent ocular evaluations and questionnaires at baseline and the 1-week visit. The primary result was reported only for the interventional arm because the primary analysis was conducted among habitual contact lens users. The observational arm therefore does not form the comparator group for the posted primary contrast; the comparator within that contrast is spectacle wear in the interventional crossover.

The registry lists enrollment of 78 and a completed study status. The primary outcome population is described as participants who successfully completed all visits in the interventional arm and did not substantially deviate from the protocol. The reported condition summaries each include 41 participants. Those figures describe the reported outcome groups and should not be interpreted as a full account of participant flow: reasons for exclusions, missing outcome measurements, and the sequence-specific analysis counts are not reported in the registry record.

The listed study start was 2019-04-09, and primary completion was 2019-06-14. The registry lists the phase as NA. It names Johnson & Johnson Vision Care, Inc. as sponsor. The registry record does not report the original sample-size justification, the planned statistical analysis in enough detail to reconstruct it, or whether the intended washout was completed as described for every participant.

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: Of the 21 subjects assigned to the observational arm, all subjects completed the study. Of the 44 subjects assigned to the interventional arm 2 subjects were discontinued. A total of 63 subjects completed the study.

Period 1

Reasons for not completing this period:

Period 2

Analysis population for the primary outcome, as defined in the registry: All subjects who had successfully completed all visits in the interventional arm and did not substantially deviate from the protocol.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All subjects who were assigned either to the interventional arm or the observational arm based on their habitual vision corrections.

6. Primary Endpoint

The registry lists the primary outcome as Non-Invasive Break Up Time (NIBUT) or Non-Invasive Keratograph Break Up Time (NIKBUT), measured over 1-Week Follow-up.

The primary endpoint is mean non-invasive break-up time (NIBUT) or non-invasive keratograph break-up time (NIKBUT), measured in seconds at the 1-Week Follow-up. It captures the interval after the final blink until distortion first appears in reflected rings, or until the participant needs to blink because of discomfort. In general, tear-film break-up measures are used to characterize how long the tear surface remains optically stable after a blink. The registry states that higher values indicate better performance on this measure.

The registry describes two measurement approaches. NIBUT may be measured by a topographer, such as Medmont, through investigator observation and a stopwatch. NIKBUT is measured by the Oculus Keratograph and reported by the instrument. Different instrumentation was used depending on site availability. The reported primary outcome combines pre-lens measurements for the interventional arm, and the registry does not provide instrument-specific results or an adjustment for measurement instrument.

This endpoint gives a focused, quantitative comparison of an ocular characteristic under the two correction conditions. A mean summarizes the central tendency of the measured times, while the standard deviation describes variation among observations. Neither summary alone describes the full distribution or determines whether the difference is important to participants. The registry record does not report a threshold for clinical importance, nor does it state how the endpoint relates to symptoms or other patient-centered outcomes.

7. Results Posted in the Registry

• Test (Senofilcon A): mean 8.28 versus 11.10 on control; difference -2.82 (95% CI -5.05 to -0.59), standardized effect d = -0.55; z-test p = 0.013.

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.

Total Scores of Meibomian Gland Expressibility (MGE)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test (Senofilcon A): mean 8.50 versus 8.50 on control; difference 0.00 (95% CI -0.55 to 0.55), 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 Test (Senofilcon A) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes concerning meibomian gland expressibility, conjunctival staining, and lid wiper epitheliopathy. The posted secondary results cover only part of the listed outcome set: the record indicates four secondary outcomes, while results are posted for one of them. The available secondary summaries do not form a consistent extension of the primary endpoint because they assess different ocular characteristics and use different outcome scales or summaries.

The available secondary results should be read as exploratory context rather than as confirmation or contradiction of the primary break-up-time finding. The primary endpoint concerns tear-film break-up time; the secondary endpoint with posted numerical results concerns meibomian gland expressibility. Similar or different patterns across these measures would not by themselves establish a common underlying effect, because they measure distinct characteristics. Results for the other listed secondary outcomes are not reported in the registry record.

Unadjusted secondary comparisons carry less weight when multiple outcomes and analyses are considered. Testing many outcomes increases the opportunity for chance findings, and the registry record does not report a multiplicity adjustment or a hierarchy specifying which secondary tests were confirmatory. Nor does it provide enough information to assess whether these results were prespecified in the analysis plan. The available results can describe what was recorded, but their statistical uncertainty and multiplicity context should temper strong conclusions.

The registry’s outcome list and posted analyses do not establish that all planned secondary measures were collected, analyzed, or omitted for a particular reason. Explanations for the difference between listed and posted outcomes are not reported in the registry record. Consequently, the secondary evidence is incomplete and should not be used to make broad claims about ocular characteristics beyond the specific measures with reported results.

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

• Total Scores of Meibomian Gland Expressibility (MGE)
• Conjunctival Staining
• Number of Eyes With Clinically Significant (Grade 3 or 4 of Overall Classification) Lid Wiper Epitheliopathy
• Meibomian Gland Expressibility (MGE) Grades

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

A mean difference expresses the average value in one condition relative to the average value in another. Here the reported direction is Test (Senofilcon A) minus Control (Spectacle), and the posted unadjusted estimate is -2.82 seconds. A negative estimate means that the test-condition mean is lower than the comparator mean. Because the registry identifies higher NIBUT/NIKBUT values as better performance, the direction of this endpoint’s difference is important to its interpretation.

A mean is useful for summarizing a continuous measure, but it compresses individual observations into one number. Participants may have values both higher and lower than the group mean. The standard deviations reported for the conditions describe the spread of observations around their respective means; they are not standard errors and do not directly give the precision of the estimated difference.

What does the confidence interval add?

A confidence interval presents a range of estimates compatible with the data and the assumptions of the analysis. It communicates uncertainty more fully than a point estimate alone. A narrower interval generally indicates greater precision, while a wider interval indicates greater uncertainty. A confidence interval is not a range containing every participant’s value, and it does not assign a probability to the true effect after the data have been observed.

The sponsor’s mixed-model analysis reports a 95% confidence interval for its least-squares mean difference. Its interpretation depends on the model and its assumptions. The registry record names the method as Mixed Model Analysis but does not report the model specification, covariance structure, handling of period and sequence, or the assumptions used for missing data. The model estimate therefore cannot be independently reconstructed from the posted record.

Why does crossover structure matter?

In a crossover design, a participant receives both conditions in different periods, with treatment order determined by randomized sequence. This structure can allow comparisons within the same participant, which can account for stable differences between participants. It also raises design-specific considerations: period effects, sequence effects, and carryover from the earlier condition may influence measurements. A washout period is intended to reduce carryover, but its presence in the design description does not demonstrate that carryover was absent.

The registry describes a 1-week washout between periods and says it was intended to eliminate potential carryover. It does not report a test for carryover, results by sequence, or the details of how period and sequence were handled in the sponsor’s model. Those omissions limit assessment of how fully the reported analysis used the crossover design. The unadjusted recalculation from condition summaries does not reproduce a paired or model-adjusted crossover analysis.

How should the p-value be read?

The recalculated p-value of 0.013 is an unadjusted test result based on the posted summary statistics. A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry’s reported mixed-model result has no p-value listed, so the recalculated p-value should not be attributed to the sponsor’s analysis.

The posted record lists multiple outcome measures and analyses. When many comparisons are examined, the chance of obtaining at least one apparently notable result can increase. Whether and how the study addressed multiplicity is not reported in the registry record. The recalculated p-value should consequently be read as an unadjusted result rather than as a multiplicity-controlled conclusion.

What does the equivalence label require?

An equivalence analysis asks whether the difference is sufficiently small to fall within limits judged acceptable in advance. This differs from simply asking whether a difference is distinguishable from zero. To interpret an equivalence result, readers need the prespecified equivalence margins, the method for defining them, and the analysis plan. Those details are not reported in the registry record. The sponsor’s mixed-model result is labeled equivalence, but the label cannot be fully evaluated without this information.

The confidence interval for the sponsor’s estimate is wholly negative, so it does not include zero. That observation alone does not determine equivalence: the relevant question is whether the interval satisfies the prespecified margins, not merely whether it includes zero. Since the margins are unavailable, the statistical basis for the registry’s equivalence label remains unclear from the record.

What can be inferred from the posted summaries?

The posted means and standard deviations support a descriptive comparison of the two conditions, and the simple recalculation supplies an unadjusted estimate and test. They do not provide participant-level data, distributional plots, or model diagnostics. It is therefore not possible to assess outliers, skewness, within-participant correlation, or the influence of individual observations from the registry summary alone.

General statistical interpretation also depends on how observations were selected for analysis and how missing measurements were handled. The stated primary population requires completion of all visits and no substantial protocol deviation. The registry record does not provide the number or reasons for exclusions from this population, details of missing measurements, or sensitivity analyses. These omissions matter because the analyzed population may differ from all randomized participants.

11. Confidence Intervals and Precision

The primary condition means are 8.28 seconds for Test (Senofilcon A) and 11.1 seconds for Control (Spectacle). Their reported standard deviations are 4.482 and 5.761 seconds, respectively. The standard deviations indicate appreciable variation in measurements around each condition mean; they should not be confused with the uncertainty in the estimated difference.

The unadjusted mean difference is -2.82 seconds. The recalculation also reports a pooled standard deviation of 5.161 seconds and a standardized difference of -0.546. These are summary-based quantities, not model-adjusted crossover estimates. The condition summaries each report 41 participants, but the registry record does not give the participant-level paired differences or the within-participant correlation needed to reconstruct a paired analysis from these summaries.

The sponsor’s mixed-model estimate is -2.79 seconds, with a 95% confidence interval from -4.14 to -1.44 seconds. This interval conveys uncertainty about the model-based average difference under the sponsor’s analysis. Its limits are on the negative side of zero, while the interval’s width still allows a range of possible magnitudes. The interval does not describe individual responses or determine whether the difference matters clinically.

Precision is also conditional on analysis choices and measurement procedures. Different instrumentation was used according to site availability, and instrument-specific results are not reported in the registry record. The model specification, equivalence margins, missing-data approach, and sequence-specific estimates are also not reported. These gaps make it difficult to judge whether the reported interval captures all relevant sources of uncertainty or whether the estimate is robust to alternative reasonable analyses.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total event counts. They are planning illustrations based on the observed effect, rather than the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 53 participants per arm for 80% power and 71 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 94 participants per arm for 80% power and 126 participants per arm for 90% power. At 50% of the observed effect, they are 211 participants per arm for 80% power and 282 participants per arm for 90% power.

In plain language, the 80% power column describes the planning size at which the assumed design would have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column uses a higher target chance of detection and therefore requires more participants for each assumed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants.

These are illustrative planning calculations, not observed power. They use the observed effect as an input and do not show the probability that this completed trial detected an effect. The registry record does not report the original design assumptions or sample-size justification, so these illustrations should not be treated as the study’s prespecified enrollment target.

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 = -2.820; pooled standard deviation σ = 5.161.
2. n = 2 × (1.96 + 0.842)² × 5.161² / -2.820² = 52.6, rounded up to 53 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 <- -2.82                      # observed difference in means
sigma <- 5.16127140344315                     # 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(3913377)
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 = 53 (80% power), 71 (90% power)
 75% of observed effect: n per arm = 94 (80% power), 126 (90% power)
 50% of observed effect: n per arm = 211 (80% power), 282 (90% power)
power.t.test: 53.6 
Simulated power at n = 53 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. Analyses Reported by the Sponsor

The sponsor’s own reported analysis is a Mixed Model Analysis, with a least-squares mean difference of -2.79 seconds and a 95% confidence interval from -4.14 to -1.44 seconds. The registry labels this result as an equivalence analysis. It does not list a p-value for the sponsor-reported result, nor does it report the equivalence margins or enough model detail to reproduce the analysis.

The simple recalculation from the posted condition summaries gives a mean difference of -2.82 seconds and p = 0.013. This is an unadjusted summary-based comparison. It is close in direction and estimate to the sponsor’s reported difference, but it is not the same analysis: the sponsor reports a model-based least-squares difference, while the recalculation does not account for the model structure of the crossover design.

The registry record does not flag a discrepancy between these estimates. The sponsor’s analysis remains the study’s reported inferential result, and the recalculation is best understood as a supplementary check of the posted summary statistics. In particular, the equivalence designation cannot be assessed without the margins and analysis details; the unadjusted p-value does not establish equivalence and should not be used as though it were the sponsor’s model-based test.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures and seven analyses, while the primary endpoint is accompanied by several secondary outcomes. When multiple outcomes or analyses are examined, the likelihood of at least one chance-positive result can rise. Common approaches include prespecifying a primary comparison, controlling the family-wise error rate, or treating secondary analyses as exploratory. The registry record does not report whether a multiplicity strategy was planned or applied.

The recalculated p-value is unadjusted. It should not be interpreted as though it accounts for the full set of outcomes and analyses. The sponsor-reported primary analysis is labeled equivalence, but the registry record does not include the margins or detailed testing procedure needed to assess that analysis. A stated analysis label and an unadjusted recalculation are not substitutes for a complete statistical analysis plan.

The primary population is defined as participants who completed all visits in the interventional arm and did not substantially deviate from the protocol. The record does not report how many randomized participants failed to meet this definition, the reasons for any exclusions, or whether all randomized participants were included in other analyses. It also does not describe missing outcome data, how missingness was handled, or whether sensitivity analyses were performed. These details are important because exclusions and missing measurements can affect both the estimate and its uncertainty.

For a crossover study, further relevant information includes the number analyzed by randomized sequence and period, whether measurements from both periods were available for each participant, and how period and sequence were modeled. The registry record does not report these details. It also does not report whether carryover was assessed or how the different measurement instruments were handled in the analysis. As a result, the posted record supports a limited reading of the reported summaries, not a full audit of the prespecified analysis or the impact of missing data and multiplicity.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry reports serious adverse events for the observational group and for the two interventional condition groups. In each listed group, the number at risk is recorded, with zero serious adverse events and zero deaths. The record also shows zero other adverse events in the listed groups. These figures describe events recorded in the registry for the stated groups and at-risk populations.

Zero recorded events does not establish that an intervention has no risk. Safety interpretation depends on how events were defined, collected, monitored, and attributed, as well as the duration and completeness of follow-up. The registry record does not report detailed adverse-event terms, event severity beyond the serious-event classification, exposure time, or a narrative account of safety monitoring. No top serious adverse-event terms are listed.

The at-risk counts differ from the primary outcome summaries, and the registry record does not explain the relationship between those populations. Safety counts therefore should not be treated as if they came from the same analysis set as the primary endpoint. They provide a description of events recorded, not a comprehensive estimate of risk or evidence about rare events.

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

The posted primary outcome shows a lower average NIBUT/NIKBUT during the contact lens condition than during spectacle wear in the reported interventional population. The unadjusted mean difference is -2.82 seconds, and the sponsor’s mixed-model estimate is -2.79 seconds. The sponsor reports a 95% confidence interval from -4.14 to -1.44 seconds and labels the analysis as equivalence. These are statistical descriptions of one measured ocular characteristic at the stated follow-up.

The result does not establish whether the size of the difference is meaningful to participants. The registry record does not report a clinical-importance threshold, a link between the measured difference and symptoms, or evidence on longer-term outcomes. The endpoint’s direction is defined in the record—higher values indicate better performance—but that does not make it a complete measure of comfort, vision, or overall ocular health.

The equivalence label should not be read as self-explanatory. Equivalence depends on prespecified limits, which are not reported in the registry record. The reported confidence interval does not include zero, but that fact alone does not determine whether the conditions meet an equivalence criterion. The unadjusted p-value also answers a different question from an equivalence analysis and does not establish that the conditions are equivalent.

The findings apply to the reported primary analysis population and the conditions and measurement procedures described in this trial. The record does not provide enough detail to determine how the result may vary by sequence, measurement instrument, or participant characteristics. It also does not support conclusions about other contact lenses, other populations, longer durations of wear, or outcomes that were not posted. Statistical results should be kept within those limits rather than turned into a general claim about treatment benefit or harm.

18. Why This Trial Matters Statistically

This trial is statistically interesting because its crossover structure creates a distinction between a simple comparison of condition means and an analysis that uses the repeated, within-participant measurements. Crossover designs can make efficient use of participants by comparing conditions across periods in the same people, but that advantage depends on appropriate handling of period, sequence, and potential carryover. The registry describes a washout period, yet the details needed to evaluate these design features are not reported.

The result also illustrates why an estimate, its uncertainty, and the purpose of the test must be interpreted together. A negative mean difference indicates the direction of the observed contrast, while the confidence interval describes uncertainty under the model. An equivalence test has a different target from a test of no difference and requires explicit margins. Without those margins, the equivalence label cannot be fully interpreted, even though a model-based estimate and interval are reported.

Measurement procedures add another layer. NIBUT and NIKBUT were obtained with different instrumentation depending on site availability, and the posted primary result combines the interventional arm’s pre-lens measurements. Without instrument-specific summaries or model details, readers cannot assess whether measurement method influenced the comparison.

Finally, this record demonstrates the value of separating the primary result from secondary findings and planning illustrations. Unadjusted secondary analyses have a different evidential role from a prespecified primary analysis, while sample-size illustrations based on an observed effect are not the same as the original trial design rationale. Distinguishing these elements helps keep conclusions aligned with what the registry actually reports.

19. 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 trial-specific limitations constrain interpretation. The primary outcome combines NIBUT and NIKBUT measurements obtained using different instruments according to site availability. The registry does not report results by instrument, site, or measurement approach, so readers cannot assess whether method differences affected the observed contrast or its precision.

The crossover design is described as having a 1-week washout intended to reduce carryover, but no sequence-specific or period-specific estimates are posted. The registry record does not report a carryover assessment, the detailed model terms, or the covariance structure. It is therefore difficult to determine how the sponsor’s mixed model handled the repeated measurements or whether relevant crossover features were incorporated.

The primary analysis population excludes participants who did not complete all visits or substantially deviated from the protocol, but participant flow and exclusion reasons are not reported. Missing-data counts, handling methods, and sensitivity analyses are also not reported. These omissions make it difficult to judge the effect of selection into the analyzed population.

The sponsor’s analysis is labeled equivalence, but the equivalence margins and their rationale are not reported. The registry also does not provide a full statistical analysis plan or the original sample-size justification. The unadjusted recalculation uses posted summaries and cannot replace those missing details. Finally, only some listed secondary outcomes have posted results, and the record does not explain the absent results or describe multiplicity control. Together, these limits call for a focused interpretation of the reported endpoint rather than broad conclusions about ocular effects.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ocular Characteristics in Contact Lens and Spectacle Wear — NCT03913377.
• Registry record last updated 2021-02-04; status last verified 2021-01.
• Results first posted 2020-08-06.
• 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.

23. Record Summary

NCT03913377, titled Ocular Characteristics in Contact Lens and Spectacle Wear, is a completed randomized, unmasked crossover study sponsored by Johnson & Johnson Vision Care, Inc. It enrolled 78 and compared spectacle wear with ACUVUE OASYS 1-Day in the interventional arm of habitual contact lens wearers. The registry describes a 2-treatment by 2-period design with a 1-week washout.

The primary endpoint was mean NIBUT/NIKBUT in seconds at the 1-Week Follow-up. The reported condition means were 8.28 seconds for Test (Senofilcon A) and 11.1 seconds for Control (Spectacle). The unadjusted recalculation gives a mean difference of -2.82 seconds and p = 0.013. The sponsor’s mixed-model analysis reports a least-squares mean difference of -2.79 seconds, with a 95% confidence interval from -4.14 to -1.44 seconds, and labels the analysis as equivalence.

The record does not report the equivalence margins, full model specification, original sample-size rationale, or detailed handling of missing data and multiplicity. Safety listings record zero serious adverse events, other adverse events, and deaths in the stated groups. Interpretation is therefore limited to the posted measures, population, and analyses.