Clinical Evaluation of Etafilcon A Contact Lenses Using a Novel Manufacturing Technology: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Evaluation of Etafilcon A Contact Lenses Using a Novel Manufacturing Technology (NCT03962790), a randomized na study. The primary outcome is Overall Comfort Score.

2. Clinical Question

3. Trial Design

The registry describes a multi-site, randomized, double-masked, 2×2 crossover study with a 1-week dispensing period. Participants were assigned to one of two sequences: Test/Control or Control/Test. Each participant wore both the test and control lenses in each eye for 1-week each, in daily disposable use, with a wash-out period of 1 week between wearing periods. The record does not report the number or locations of study sites.

The listed enrollment was 95. The primary outcome summaries include 89 for the test condition and 89 for the control condition. Because this is a crossover design, those condition-specific counts should not be added to infer a number of distinct participants. The registry record does not explain the relationship between the enrollment figure and the condition-specific outcome counts.

The study status is completed. The recorded start was 2019-05-15, and primary completion was 2019-07-10. The record lists the study phase as NA. It identifies Johnson & Johnson Vision Care, Inc. as sponsor and lists Visual Acuity as the condition.

A crossover design lets participants contribute observations under both conditions, so within-person comparisons may be relevant to analysis. The registry record does not report the statistical method used for the sponsor’s analysis, or whether its model accounted for pairing, period, sequence or possible carryover. The randomization method and details of masking procedures are also not reported in the registry 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.

Before assignment: A total of 95 participants were enrolled in this study however one participant was never randomized due to screen failure therefore, 94 participants were randomized to receive study drug.

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 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.

6. Primary Endpoint

The registry lists the primary outcome as Overall Comfort Score, measured over 1-Week Follow-up.

The primary endpoint was Overall Comfort Score at 1-Week Follow-up, measured in units on a scale. It was assessed with the Contact Lens User Experience (CLUE) questionnaire, a validated patient-reported outcomes questionnaire described in the registry as assessing comfort, vision, handling and packaging among soft contact lens wearers in the US, ages 18-65. The primary outcome population was subjects who successfully completed all visits and did not substantially deviate from the protocol.

The posted endpoint summaries use means and standard deviations. The registry explains that derived CLUE scores use Item Response Theory and follow a normal distribution, with a population average score of 60 and standard deviation 20. Higher scores indicate a more favorable or positive response. It also states that a 5-point increase in an average CLUE score translates into a 10% shift in the score distribution for the population of soft disposable contact lens wearers.

Patient-reported comfort is useful because it records participants’ experience rather than relying only on a technical or clinical measurement. It is nevertheless one defined aspect of lens experience. A difference in this score would not by itself describe every aspect of vision, handling, packaging or safety. The registry record does not report a minimally important difference for this trial or the non-inferiority margin used for its reported non-inferiority analysis.

7. Results Posted in the Registry

• Etafilcon A Test for Novel: mean 56.52 versus 55.72 on control; difference 0.80 (95% CI -5.55 to 7.15), standardized effect d = 0.04; z-test p = 0.805.

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.

Average Daily Wear Time

• 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 Test for Novel: mean 14.22 versus 14.16 on control; difference 0.06 (95% CI -0.50 to 0.62), standardized effect d = 0.03; z-test p = 0.833.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Etafilcon A Test for Novel and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the registry are LogMAR Visual Performance Scale and Average Daily Wear Time. Detailed numerical results and comparisons are posted for Average Daily Wear Time; the registry record does not provide comparable detailed results for the LogMAR Visual Performance Scale. Across the reported comparisons, the overall pattern is that the condition means are close and the unadjusted intervals include zero. This general pattern aligns with the primary comfort comparison in the limited sense that neither recalculated comparison precisely separates the condition means.

Average daily wear time is a different aspect of the wearing experience from questionnaire-reported comfort. It can add context, but it does not measure comfort directly and should not be treated as a substitute for the primary outcome. Nor does agreement in broad direction across outcomes establish that the conditions are equivalent. Each outcome has its own measurement scale, uncertainty and analysis.

The registry lists four outcome measures and five analyses, while two secondary outcomes are posted. The record does not explain the relationship between these counts or provide the full set of analysis details. In particular, a complete prespecified analysis plan and multiplicity adjustment are not reported in the registry record.

Unadjusted secondary results generally carry less confirmatory weight when several outcomes or analyses are considered. Without a reported adjustment, a result should be interpreted as exploratory or descriptive rather than as decisive evidence on its own. This caution applies even when a secondary estimate appears consistent with the primary pattern. The registry’s reported secondary data offer limited supporting context, but do not resolve the uncertainty around the primary comparison or the missing non-inferiority details.

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

• LogMAR Visual Performance Scale
• Average Daily Wear Time

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome and the secondary outcome of average daily wear time are continuous measures. Their condition summaries are reported as means and standard deviations. A mean describes the arithmetic average of the observed scores or hours; a standard deviation describes how dispersed individual values are around that average. Neither summary alone captures all details of the observed distribution.

What does a mean difference express?

A mean difference expresses the test-condition mean minus the control-condition mean in the units of the outcome. A positive estimate means the test mean is higher; a negative estimate means it is lower. For comfort, the measure is units on a scale. For average daily wear time, the unit is hours. The estimate is not itself a measure of certainty: its interval gives a range of values compatible with the analysis and data, under the analysis assumptions.

The posted recalculations are described as simple, unadjusted calculations from summary statistics. They compare condition means without reporting an adjustment for other variables. For the primary endpoint, the recalculated difference is 0.8; for average daily wear time, it is 0.06. These estimates should not be conflated with the registry’s sponsor-reported posterior mean differences. The registry does not provide the method for the latter analysis.

Why does the crossover structure matter?

In a crossover study, the same participant receives both conditions at different times. Observations from one participant may be more alike than observations from different participants. An analysis that uses the within-participant relationship can therefore differ from one that treats condition summaries as if they came from independent groups. Period and sequence may also be relevant, and carryover from an earlier wearing period can be considered in study design and analysis.

The registry reports random assignment to Test/Control or Control/Test and a 1-week wash-out period between wearing periods. It does not state whether the sponsor’s analysis modeled within-participant pairing, period, sequence or carryover. The summary-statistic recalculations are unadjusted and do not incorporate those features. They offer a transparent comparison of the posted means, but they are not a substitute for a reported crossover-specific model.

What do a confidence interval and a p value tell readers?

A confidence interval conveys uncertainty around an estimate. A wider interval indicates less precision than a narrower interval on the same scale. If an interval for a difference includes zero, values compatible with the data include no difference as well as differences in either direction. This does not establish that the conditions are equal; it means the estimate alone does not distinguish those possibilities precisely.

A p value summarizes how unusual the observed data, or more extreme data, would be under a particular null hypothesis and analysis model. It depends on the model and assumptions. An unadjusted p value does not account for testing multiple outcomes or analyses. It also does not indicate the probability that a result will replicate or the clinical importance of the estimated difference.

What is distinctive about the reported non-inferiority analysis?

Non-inferiority analyses ask whether an outcome under one condition is not worse than the comparator by more than a prespecified acceptable margin. The margin is essential: the estimate and its uncertainty must be evaluated relative to that threshold. The registry labels the sponsor’s reported analyses as non-inferiority and gives posterior mean differences with 95% confidence intervals, but the margin, statistical method and decision rule are not reported in the registry record. The label alone is not enough to determine whether a non-inferiority conclusion follows.

The registry describes CLUE scores as derived with Item Response Theory and as following a normal distribution in the reference population. That description does not establish the distribution of scores in this trial or the method used to compare conditions. The reported means and standard deviations support descriptive interpretation, while the details needed to reproduce or fully assess the sponsor’s analysis are not reported.

How should secondary outcomes be treated?

Secondary outcomes can provide supporting context about other measured aspects of the study. They generally carry less confirmatory weight when multiple outcomes or analyses are considered and no adjustment for multiplicity is reported. An unadjusted result may be less persuasive as confirmatory evidence because the chance of observing at least one apparently notable result can rise when many questions are tested. This is a general statistical consideration, not a claim about an unreported analysis plan for this trial.

11. Confidence Intervals and Precision

For the primary comfort comparison, the simple unadjusted mean difference is 0.8, and its interval extends from -5.552 to 7.152. This interval includes zero, so the posted summary is compatible with no difference as well as with a lower or higher average score for the test condition. Its width indicates that the estimated difference is not sharply pinned down by this recalculation. The registry record does not provide a trial-specific threshold for a meaningful difference, so the interval cannot be classified against such a threshold.

The sponsor-reported non-inferiority analysis gives a posterior mean difference of 0.09 and a 95% confidence interval from -4.37 to 4.65. That interval also spans zero. Its interpretation for non-inferiority depends on the margin and method, which are not reported in the registry record. The sponsor’s interval and the recalculated interval come from different reported approaches and should not be treated as interchangeable.

For average daily wear time, the unadjusted mean difference is 0.06 hours, with an interval from -0.499 to 0.619. This range includes zero and allows values on either side of it. The estimate is therefore uncertain even though the condition means are close.

In general, confidence intervals communicate both direction and precision; they do not guarantee that the true effect lies within the displayed limits, and they do not determine clinical importance on their own. The recalculated intervals are based on posted summary statistics and do not report a crossover-specific adjustment. The registry record does not report the method or other assumptions needed to reproduce the sponsor’s posterior intervals. Precision should therefore be considered alongside the design, analysis details and missing information, rather than inferred from the point estimates alone.

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 estimates are stated as participants per arm, not total events. They are illustrations based on the observed effect, not the assumptions used to design this trial. The registry record does not report the trial’s original sample-size justification or design assumptions.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. For each effect assumption, the 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting that specified effect under the planning assumptions. The 90% power column gives the corresponding estimate for a 90% chance. These are prospective planning quantities, not observed results.

The estimates include planning for 100% of the observed effect, 75% of the observed effect and 50% of the observed effect. The listed participants-per-arm estimates rise as the assumed effect becomes smaller. This follows a general statistical principle: smaller differences are harder to distinguish from random variation and usually require more participants to detect at a given power level.

These calculations are based on a simple two-arm planning framework and do not report adjustment for the crossover structure. They should not be read as a reconstruction of how the completed study was designed, nor as a recommendation for a future study without considering its design and analysis. This is not observed power: it is a planning illustration using the observed effect as an input, not a measure of the probability that the completed study detected an effect.

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 = 0.800; pooled standard deviation σ = 21.621.
2. n = 2 × (1.96 + 0.842)² × 21.621² / 0.800² = 11,465.6, rounded up to 11,466 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 <- 0.800000000000004                      # observed difference in means
sigma <- 21.6206804934535                     # 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(3962790)
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 = 11,466 (80% power), 15,350 (90% power)
 75% of observed effect: n per arm = 20,384 (80% power), 27,288 (90% power)
 50% of observed effect: n per arm = 45,863 (80% power), 61,397 (90% power)
power.t.test: 11466.6 
Simulated power at n = 11,466 per arm: 0.803 (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 registry reports the sponsor’s primary non-inferiority analysis as a posterior mean difference of 0.09, with a 95% confidence interval from -4.37 to 4.65. For average daily wear time, it reports a posterior mean difference of 0.02, with a 95% confidence interval from -0.32 to 0.34. No p values or analysis methods are listed for these reported analyses, and the registry record does not report the non-inferiority margin.

The simple unadjusted recalculations are separate comparisons derived from the posted condition means and standard deviations. They produce a primary mean difference of 0.8 and an average daily wear time difference of 0.06 hours, each with its own interval. Different estimates can arise when analyses use different methods or model structures. The registry does not provide enough detail to determine exactly why the sponsor-reported estimates differ from the summary-statistic recalculations.

The recalculations do not replace the sponsor’s analysis and should not be interpreted as a replication of it. Conversely, the non-inferiority label does not by itself establish that the criterion was met: that assessment needs the margin and relevant analysis details. Because the registry does not report those details, the sponsor’s result can be described as posted, but its non-inferiority conclusion cannot be independently evaluated from this record alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when researchers assess more than one outcome, comparison or analysis. Each additional test creates another opportunity for a result to appear notable by chance under its null model. An unadjusted p value describes a single comparison under its assumptions; it does not account for the broader set of questions examined. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting outcomes.

The registry lists four outcome measures and five analyses and identifies two secondary outcomes as posted. The record does not explain how all of these measures and analyses relate to one another, which outcomes were prespecified as confirmatory, or how any multiplicity would be handled. The available unadjusted secondary comparisons should therefore be interpreted cautiously and should not be treated as independent confirmation of the primary result.

The primary outcome population is described as subjects who completed all visits successfully and did not substantially deviate from the protocol. This defines the population for the posted primary outcome, but the registry record does not report how many enrolled participants were excluded from that population or the reasons for any exclusions. It also does not report the handling of missing observations, incomplete questionnaires, withdrawals or deviations beyond the population description.

The registry record does not report whether analyses followed intention-to-treat, per-protocol or another named analysis principle, nor does it describe imputation or sensitivity analyses for missing data. These omissions matter because excluding participants or handling incomplete observations in different ways can affect the analysis population and estimates. For a crossover study, details of period-specific availability and within-participant pairing would also help readers assess how the available observations informed the comparison. Those details are not reported in the registry record.

These gaps limit assessment of the robustness and confirmatory status of the posted results. They do not show that a particular analysis was inappropriate; they mean that the registry record does not contain the information needed to evaluate these aspects fully.

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 test condition among 93 at risk, with 0 affected, and for the control condition among 90 at risk, also with 0 affected. The reported other adverse events were likewise 0 among 93 at risk for the test condition and 0 among 90 at risk for the control condition. Deaths are reported as 0 in both conditions. These figures describe the safety entries posted for the trial.

Zero reported events in these groups means that the registry lists no affected participants in the reported categories during the recorded study. It does not establish that the risk of an event is absent, or rule out events too uncommon to be observed in this study. The trial involved short wearing periods, and the registry record does not provide event-term details, severity information for other adverse events, or additional follow-up safety information. No serious adverse event terms are listed.

The at-risk counts differ from the condition-specific outcome counts, and the registry does not explain the difference. In a crossover design, condition-specific safety reporting may not correspond to mutually exclusive groups of participants. The at-risk counts should not be added to infer a number of distinct participants. Safety findings should be understood within the populations and reporting period recorded, not as a complete estimate of longer-term or rare-event risks.

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

The results describe average comfort scores and average daily wear time for the novel and current lens conditions in this randomized, double-masked crossover study. The posted condition means are similar in magnitude, and the simple unadjusted comparisons have intervals that include zero. This indicates uncertainty about the direction and size of the differences, not proof that the conditions are identical.

The registry’s separate non-inferiority analyses are labeled as such, but the margin and methods are not reported. Without those details, readers cannot determine whether the sponsor’s prespecified non-inferiority criterion was satisfied. The reported posterior differences and intervals should be presented as results in the record, rather than treated as a complete basis for a non-inferiority conclusion.

The findings concern the measured outcomes during the short wearing periods described. They do not establish results for longer use, other patient populations, other contact lens products or outcomes not reported. Comfort is one patient-reported dimension of lens experience; the results do not by themselves settle questions about visual performance, handling, packaging or broader safety.

The safety record lists no serious or other adverse events in the posted categories and no deaths. Such entries are reassuring as descriptions of the observed record, but cannot demonstrate that uncommon events never occur or establish longer-term safety.

Statistically, the central message is one of limited precision and incomplete analysis detail. The mean estimates and intervals describe the available summaries, but the crossover-specific sponsor method, non-inferiority margin, missing-data approach and multiplicity handling are not reported in the registry record. Those limits should accompany any account of what the results mean.

18. Why This Trial Matters Statistically

This trial is a useful example of why study design and statistical interpretation cannot be separated. A crossover design gives each participant experience with both conditions, which can support within-person comparisons. At the same time, the analysis needs to reflect the paired observations and potentially relevant period and sequence effects. The registry describes the sequence assignment and wash-out period, but does not report whether the sponsor’s model accounted for these features.

It also illustrates the difference between an estimate and the certainty around it. The primary recalculated mean difference is small compared with the span of its interval, which includes values on both sides of zero. A point estimate alone can make a result seem more definite than the accompanying uncertainty warrants. Similarly, an interval that includes zero is not evidence of equivalence without a suitable equivalence or non-inferiority framework.

The reported non-inferiority analysis highlights the importance of a prespecified margin. A non-inferiority label is not sufficient to assess a claim when the margin, method and decision rule are absent from the registry record. The sponsor’s reported analysis and a simple summary-statistic recalculation answer questions through different approaches and should be kept distinct.

Finally, this record shows why multiplicity, analysis populations and missing data matter. Unadjusted secondary results can contribute context, but they provide less confirmatory support when the broader analysis plan is not reported. Transparent methods and clear reporting of exclusions, missing observations and safety follow-up help readers judge how much weight to place on statistical estimates.

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.

The main trial-specific limitation in interpreting the numerical comparisons is that the registry does not report the method used for the sponsor’s analyses. In a crossover design, readers would benefit from knowing how the analysis handled paired observations, period, sequence and possible carryover. The existence of a wash-out period is recorded, but its adequacy cannot be assessed from the registry record.

The registry identifies the sponsor’s analyses as non-inferiority analyses but does not report the margin or the method. This prevents an independent assessment of whether the reported intervals satisfy the intended criterion. The simple unadjusted recalculations provide a comparison based on condition summaries, but they do not represent a reported crossover-specific analysis.

The record does not describe the handling of missing outcome data, the number or reasons for exclusions from the primary outcome population, or sensitivity analyses. It also does not report multiplicity procedures or a complete hierarchy for the outcome measures and analyses. These omissions limit assessment of how robust or confirmatory the findings are.

The primary outcome reflects a 1-Week Follow-up, and the study describes 1-week wearing periods. The registry record does not provide longer-term outcome results. The CLUE endpoint captures a defined patient-reported experience and cannot stand for every aspect of lens performance or safety. Although the record lists Visual Acuity as the condition and includes a LogMAR Visual Performance Scale among secondary outcomes, detailed numerical results for that secondary measure are not presented in the posted outcome details.

Safety reporting lists no events in the specified categories, but the record does not provide event-term detail or longer-term follow-up. These limitations concern what can be assessed from the registry record; they do not establish that unreported procedures or analyses were not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Evaluation of Etafilcon A Contact Lenses Using a Novel Manufacturing Technology — NCT03962790.
• Registry record last updated 2020-08-12; status last verified 2020-08.
• Results first posted 2020-08-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03962790 is a completed, randomized, double-masked, multi-site crossover study of Etafilcon A Test for Novel and Etafilcon A Control for Current, both listed as 1-DAY ACUVUE® MOIST. Participants were assigned to Test/Control or Control/Test sequences, with each condition worn in both eyes for 1-week and a 1-week wash-out between periods.

The primary outcome was Overall Comfort Score assessed with the CLUE questionnaire at 1-Week Follow-up. The registry also posts average daily wear time results and describes sponsor-reported non-inferiority analyses. The simple recalculations show intervals spanning zero, while the non-inferiority margin and analysis methods are not reported in the registry record.

Safety entries list 0 serious adverse events, 0 other adverse events and 0 deaths in each condition’s reported group. Missing-data handling, multiplicity procedures and several analysis details are not reported, limiting independent evaluation of the results.