Visual Performance of Soft Contact Lenses With Myopia Control Optics: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Visual Performance of Soft Contact Lenses With Myopia Control Optics (NCT05141448), a randomized phase not stated study. The primary outcome is Binocular Visual Performance (LogMAR).

2. Clinical Question

3. Trial Design

The registry record describes a randomized, single-masked, controlled, bilateral, dispensing study with a 3x3 crossover model and a run-in period. In a crossover design, participants receive multiple study conditions in a planned sequence, so comparisons can use measurements collected under more than one lens condition. The sequence is part of the design; it does not mean that each lens was studied in a separate parallel group.

Eligible subjects were to wear the run-in lens for approximately one week before being randomized to a sequence of Test 1, Test 2, and Control. The six listed sequences vary the order of those conditions. The run-in lens was Etafilcon A, Test 1 was Senofilcon A C3 (EMO-118), Test 2 was Senofilcon A C3 (EMO-114), and the control was Omafilcon A (MS1D). The record lists additional intervention names, including 1-Day Acuvue Moist and MiSight® 1 day, but does not explain their relationship to all sequence labels.

Enrollment was 79, and the study status is completed. The study start date was 2021-11-22, and primary completion was 2022-04-01. The posted primary endpoint population was subjects who successfully completed all study visits without a major protocol deviation. Endpoint summaries list 49 observations for each lens condition. The registry record does not explain the relation between the enrollment count and the endpoint analysis population, or report how sequence allocation was balanced.

Visual performance was assessed at the 2-week follow-up visit; the run-in lens measurement was taken at the 1-week follow-up visit. The record says the study was single-masked but does not identify who was masked. It also does not report the washout arrangements, sequence-specific results, or details of how period and carryover effects were handled.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Period 1

Reasons for not completing this period:

Period 2

Reasons for not completing this period:

3

Reasons for not completing this period:

4

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects who successfully completed all study visits without a major protocol deviation.

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 dispensed a study lens.

6. Primary Endpoint

The registry lists the primary outcome as Binocular Visual Performance (LogMAR), measured over Up to 2-Week Follow-up.

The primary endpoint was binocular visual performance, measured as contact-lens-corrected distance visual acuity on the logarithm of the minimum angle of resolution scale, or logMAR. Measurements were taken under high-luminance, high-contrast conditions at 4 meters using ETDRS charts. The reported outcome is the mean for each lens type, with standard deviation as the measure of spread.

LogMAR provides a numerical scale for visual acuity. The record states that lower values indicate better vision and that 0.0 logMAR is equivalent to 20/20 Snellen visual acuity. The endpoint therefore allows the study to compare average visual performance among the test lenses and control in the specified viewing conditions. A mean difference describes the separation between two reported averages; its direction must be read alongside the scale’s meaning, because a higher logMAR value corresponds to poorer visual acuity.

The primary lens measurements were collected at the 2-week follow-up visit. The run-in lens was measured at the 1-week follow-up visit. These are not measurements at the same visit, so the run-in result should not be read as if it were another observation collected at the same scheduled endpoint visit. The registry record does not report other primary endpoints. The stated endpoint population includes subjects who completed all study visits without a major protocol deviation, rather than an explicitly described intention-to-treat population.

7. Results Posted in the Registry

• Run-in: Etafilcon A: mean -0.10 versus -0.11 on control; difference 0.01 (95% CI -0.01 to 0.03), standardized effect d = 0.17; z-test p = 0.394.
• Senofilcon A C3 (EMO-114) [Test 2]: mean -0.10 versus -0.11 on control; difference 0.01 (95% CI -0.01 to 0.03), standardized effect d = 0.16; z-test p = 0.417.
• Senofilcon A C3 (EMO-118) [Test 1]: mean -0.07 versus -0.11 on control; difference 0.04 (95% CI 0.02 to 0.06), standardized effect d = 0.65; z-test p = 0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean difference represent?

The endpoint is continuous, so it can be described by a mean and a standard deviation. A mean is the average of the recorded values within a lens condition. A mean difference compares two such averages, with the first condition’s mean compared against the control mean in the posted recalculations. A difference of zero would mean the two reported means are equal. The sign indicates direction, and for this outcome that direction must be interpreted using the rule that lower logMAR values indicate better vision.

The recalculations compare the posted group-level means and standard deviations. They are unadjusted comparisons, not a reconstruction of the trial’s complete crossover analysis. In a crossover study, the same participant may contribute measurements under several conditions. A model can account for the way measurements within a participant are related, as well as design features such as condition and period. The registry identifies a linear mixed model for the sponsor’s EMO-118 versus control analysis, but does not report its full specification. The unadjusted recalculation therefore serves as a transparent comparison of the posted summaries, not as a replacement for the sponsor’s model.

What does a standard deviation describe?

A standard deviation describes how spread out individual recorded values are around their group mean. It is not the uncertainty of the mean itself, and it is not a confidence interval. The posted standard deviations range from 0.057 to 0.064. They describe variability in the outcome values within the stated lens-condition summaries; they do not show how the study handled repeated measurements or possible correlations among them. A more complete account of variability in a crossover analysis would depend on model details that are not reported in the registry record.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the estimate under the statistical method and its assumptions. The recalculated intervals are based on summary statistics, while the sponsor’s interval is reported from a linear mixed model. The two methods do not necessarily encode the same assumptions about the crossover data. An interval that includes zero indicates that a zero mean difference lies within that interval; an interval that does not include zero indicates that zero is outside it under that calculation. Neither observation, by itself, states whether a difference is clinically important.

The sponsor’s interval for the non-inferiority analysis has a separate interpretive requirement. Non-inferiority is assessed against a prespecified margin, which defines the amount of difference accepted for that question. The margin and the sponsor’s detailed decision rule are not reported in the registry record. It would therefore be inappropriate to infer a non-inferiority conclusion just from the reported label, estimate, and interval.

Why can over-dispersion matter?

In general, over-dispersion means that the observed variability is greater than a model’s assumed variability. It matters because standard errors and confidence intervals can be too narrow if the model underestimates variability. This endpoint is continuous and is reported with standard deviations; the registry does not describe an over-dispersion assessment or identify it as a concern. The concept is a general statistical consideration, not a reported finding for this trial.

What does randomization contribute?

Random allocation to sequences is intended to reduce systematic differences in assigned order. In crossover studies, randomizing sequence can help separate treatment-condition effects from order effects, if the analysis also addresses the relevant design features. The record describes randomization and lists six sequences. It does not report the sequence allocation counts, whether allocation was balanced, or the exact method used to account for sequence, period, and within-participant correlation. Those details are important for assessing how the randomization was reflected in the analysis.

What can the p-values tell readers?

The p-values of 0.394, 0.417, and 0.001 are unadjusted results from the summary-statistic recalculations, not sponsor-reported p-values. A p-value describes how compatible the observed data are with a specified null model, assuming the analysis assumptions hold. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of a difference. The registry does not report a multiplicity adjustment for the comparisons. Since multiple comparisons are present in the recalculated summaries, the unadjusted p-values should be read as individual comparisons rather than as an adjustment for testing several outcomes or contrasts.

The sponsor’s mixed-model result reports no p-value. The recalculated values should not be substituted for one because the method and estimand are not identical in the information available. The registry record also does not report the complete statistical analysis plan, model covariates, handling of missing observations, or any planned interim analyses. These omissions leave uncertainty about the full prespecified analysis strategy.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: a narrower interval indicates a more tightly estimated value under the method used, while a wider interval leaves more uncertainty about the estimate. The recalculated 95% interval for EMO-118 versus control is 0.016 to 0.064 around a mean difference of 0.04. The recalculated interval for EMO-114 versus control is -0.014 to 0.034 around a difference of 0.01, and the run-in versus control interval is -0.013 to 0.033 around a difference of 0.01.

The EMO-114 and run-in intervals include zero; their ranges are compatible with a small difference in either direction as well as no difference under the recalculation. The EMO-118 interval lies above zero in the unadjusted calculation. That does not on its own determine whether the magnitude matters clinically, and it does not resolve the sponsor’s non-inferiority question. Interpretation of non-inferiority requires a margin, which is not reported in the registry record.

The sponsor reported a 95% confidence interval from 0.02 to 0.06 for its linear mixed model estimate of 0.04. This interval is rounded differently and comes from a different analysis than the unadjusted recalculation. Its precision should be understood in the context of that model, whose full specification is not reported. A confidence interval captures statistical uncertainty conditional on the data and method; it does not account for every possible source of uncertainty, such as missing outcomes, deviations from model assumptions, or limitations in the study population.

The endpoint summaries report standard deviations, but no confidence intervals for each lens-specific mean. The endpoint count of 49 for each condition does not by itself describe the effective information available for a crossover comparison, because within-participant dependence and analysis details matter. The registry does not provide sequence-specific estimates or enough model information to assess those aspects independently.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrative sample-size calculations based on the observed mean difference and the stated fraction of that effect. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. These are planning assumptions for the illustration, not the original design assumptions of the trial. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to be needed for an 80% chance of detecting the specified effect under those planning assumptions, if that effect is real and the assumptions hold. The 90% power column gives the corresponding estimate for a 90% chance. These describe prospective design scenarios; they do not say what power the completed trial actually had.

Each comparison has three planning scenarios: planning for 100%, 75%, or 50% of the observed effect. As the target effect becomes smaller, it is harder to distinguish from random variation, so more participants are needed. For example, the figures for planning for 50% of the observed effect are larger than those for planning for the full observed effect within each comparison. The estimates differ among comparisons because the observed effects and variability differ.

These calculations use an equal-allocation, two-arm framework and a normal approximation. They do not reproduce a crossover design analysis, and the registry record does not report a trial-specific design calculation that could be compared with them. They are not observed power: observed power is not a substitute for interpreting the estimated effect and its confidence interval. The planning figures are best read as illustrations of the sample sizes that would be associated with those hypothetical target effects under the listed assumptions.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = 0.010; pooled standard deviation σ = 0.058.
2. n = 2 × (1.96 + 0.842)² × 0.058² / 0.010² = 528.2, rounded up to 529 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 <- 0.01                      # observed difference in means
sigma <- 0.0580086200490927                     # 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(5141448)
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 = 529 (80% power), 708 (90% power)
 75% of observed effect: n per arm = 940 (80% power), 1,258 (90% power)
 50% of observed effect: n per arm = 2,113 (80% power), 2,829 (90% power)
power.t.test: 529.2 
Simulated power at n = 529 per arm: 0.807 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Analyses Reported by the Sponsor

The sponsor reported a linear mixed model analysis of EMO-118 versus the control, with a mean difference of 0.04 and a 95% confidence interval from 0.02 to 0.06. The comparison was labelled non-inferiority. The registry record does not include a p-value for that analysis, the non-inferiority margin, or the full model specification. Without the margin and decision rule, the reported estimate and interval do not establish on their own whether the non-inferiority criterion was met.

The recalculated comparison uses the posted means and standard deviations and gives a mean difference of 0.04, a 95% confidence interval from 0.016 to 0.064, and an unadjusted p-value of 0.001. The estimate is the same at the reported precision, while the confidence interval differs in its endpoints because the calculation is not the sponsor’s linear mixed model. The registry record does not flag a discrepancy, but the two analyses should still be distinguished by their methods and purpose.

The recalculation is a simple unadjusted comparison of summary statistics. It does not incorporate the sponsor’s mixed-model structure or establish the sponsor’s non-inferiority decision. The sponsor’s reported model result is the relevant record of the sponsor’s own analysis; the recalculated result is supplementary context based on the posted summaries. No sponsor analysis for the other two recalculated contrasts is reported.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified as binocular visual performance in logMAR, and the primary endpoint population is described as subjects who completed all study visits without a major protocol deviation. The registry reports one outcome measure and one analysis. The record does not give a detailed statistical analysis plan, identify a multiplicity procedure, or say whether any adjustment was applied across comparisons. The recalculated p-values are therefore unadjusted and should not be interpreted as family-wise or otherwise multiplicity-controlled results.

The sponsor’s reported analysis is specifically a non-inferiority comparison of EMO-118 with control. The registry does not report the non-inferiority margin, the rationale for that margin, the testing sequence, or the decision rule. It also does not report whether the other lens comparisons were confirmatory or exploratory. These omissions matter because the interpretation of multiple contrasts depends on which questions were prespecified and how error across tests was addressed.

The endpoint population definition excludes subjects who did not successfully complete all visits or had a major protocol deviation, but the record does not report how many subjects were excluded for either reason or how missing measurements were handled. It does not describe imputation, model-based handling of incomplete observations, or sensitivity analyses. The posted endpoint summaries list 49 for each condition, while the enrollment count is 79; the registry does not explain the relationship between these figures.

The record also does not state whether the analyses were intention-to-treat, per-protocol, or another named analysis population, beyond the endpoint’s completion and protocol-deviation description. It does not report interim analyses, stopping rules, or an independent data monitoring approach. These items are not necessarily absent from the conduct of the trial; they are not reported in the registry record. As a result, readers cannot determine from the posted information how missing data, protocol deviations, and multiple testing were handled in the complete prespecified analysis.

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 5% reporting threshold.

The registry safety summaries report zero serious adverse events in each listed lens group. The at-risk counts were 75 for Etafilcon A run-in, 69 for EMO-114, 70 for EMO-118, and 69 for Omafilcon A. The registry also reports zero other adverse events in each group, with those same group-specific at-risk counts. Deaths are reported as zero in every group.

These are group-level counts as recorded in the safety summary. They are not the same set of counts as the endpoint summaries, which report 49 for each lens condition. The registry does not explain the relationship between safety and endpoint populations, or provide event descriptions because no serious-event terms are listed. Zero reported events means none were recorded in these summaries; it does not establish that the risk of an event is absent or that rare events could not occur. The safety record should be read as a description of events recorded during this study, not as a broad comparison of safety across all settings or populations.

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

The results describe average binocular, contact-lens-corrected distance visual acuity under high-luminance, high-contrast conditions, measured with ETDRS charts at 4 meters and the specified follow-up visits. The endpoint is narrow: it concerns visual performance in that testing context, not every aspect of vision, comfort, wear experience, or myopia control. Lower logMAR values indicate better vision, and the record identifies 0.0 logMAR as equivalent to 20/20 Snellen visual acuity.

The posted means and recalculated contrasts show that the EMO-118 mean was higher than the control mean on the logMAR scale, while EMO-114 and run-in comparisons had smaller positive estimated differences. The uncertainty intervals for the latter two recalculations include zero. The unadjusted EMO-118 interval does not include zero, but that result is not the sponsor’s mixed-model analysis and is not itself a non-inferiority conclusion. The sponsor’s estimate and confidence interval must be considered in relation to the non-inferiority margin, which is not reported.

The results do not establish whether a difference is practically important. The registry record does not give a threshold for a clinically meaningful change, and it does not report the non-inferiority margin. Nor do these results establish a conclusion about long-term myopia control: the posted primary endpoint is visual acuity, and no secondary endpoint results are reported.

The record also does not show how sequence, period, missing data, and within-participant correlations were addressed beyond identifying the sponsor’s linear mixed model for one comparison. The displayed summary estimates therefore need to be interpreted with their analysis limitations in mind. The endpoint population is restricted to subjects who completed all study visits without a major protocol deviation, and the record does not explain the relationship between that population and the overall enrollment.

In short, the registry supplies numerical descriptions of visual acuity under specified conditions, together with one sponsor-reported non-inferiority model result. It does not supply all the design and analysis details needed for a complete independent evaluation of the non-inferiority claim or broader clinical interpretation.

17. Why This Trial Matters Statistically

This trial illustrates why the design and endpoint matter as much as the point estimate. A crossover study exposes participants to more than one lens condition in a planned sequence, whereas the posted means and simple recalculations look like separate condition summaries. A crossover model can account for repeated measurements within a participant and for design features such as period. The sponsor reports a linear mixed model for one comparison, but the full specification is not reported. Readers therefore need to keep the sponsor’s model-based result distinct from an unadjusted comparison of summary statistics.

The meaning of the outcome’s direction is also important. LogMAR is not a scale on which a larger value automatically means better performance: the record explicitly states that lower values indicate better vision. Describing the sign of a difference without explaining the scale can therefore lead to a mistaken reading.

The non-inferiority label raises a further statistical issue. A non-inferiority question depends on a margin specified in advance, and the registry record does not report that margin. A point estimate and confidence interval are not sufficient to determine the conclusion without knowing the criterion they are being compared with. This is a useful reminder that a model result’s label does not replace the information needed to interpret its decision rule.

Finally, the planning illustrations are not a retrospective measure of the trial’s success or failure. They show how hypothetical target effects relate to sample-size requirements under stated assumptions, while the original design assumptions are not reported. Together, these features make the record a practical example of separating descriptive results, recalculated comparisons, sponsor analyses, and design-planning scenarios.

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.

The registry record leaves important details unavailable for independent appraisal. It does not report the non-inferiority margin, the full mixed-model specification, the allocation counts by sequence, or how period and sequence effects were handled. It also does not report whether washout was used or how possible carryover effects were assessed. These are particularly relevant details for interpreting a crossover study.

The endpoint population is defined by completion of all visits without a major protocol deviation, but the record does not explain exclusions, missing measurements, or the relationship between the endpoint summaries and the enrollment count. The group-specific endpoint summaries report 49, while enrollment is 79. No intention-to-treat analysis, missing-data method, or sensitivity analysis is described. The safety summaries use different at-risk counts, and their relationship to the endpoint population is not explained.

The record reports one sponsor analysis for EMO-118 versus control, but no sponsor results for the other recalculated contrasts. It does not report multiplicity handling, a detailed analysis plan, interim analyses, or the original sample-size justification. It also does not identify who was masked in the single-masked design. The primary endpoint focuses on visual acuity under high-luminance, high-contrast conditions and does not represent broader visual outcomes or myopia-control effectiveness. These are limitations of the registry information available for interpretation, and do not necessarily establish that the unreported procedures were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Visual Performance of Soft Contact Lenses With Myopia Control Optics — NCT05141448.
• Registry record last updated 2025-04-27; status last verified 2025-04.
• Results first posted 2025-04-08.
• 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

NCT05141448 is a completed randomized, single-masked, controlled 3x3 crossover study of visual performance with soft contact lenses with myopia control optics. The registry lists enrollment of 79 and describes a run-in period followed by randomized sequences of Test 1, Test 2, and Control. The primary outcome is mean binocular visual acuity in logMAR under high-luminance, high-contrast conditions. Lower values indicate better vision.

The sponsor reported a linear mixed model non-inferiority analysis for EMO-118 versus control, with a mean difference of 0.04 and a 95% confidence interval from 0.02 to 0.06. A simple unadjusted recalculation gives the same estimate at the reported precision, with a 95% confidence interval from 0.016 to 0.064. The registry does not report the non-inferiority margin or full model specification. It reports zero serious adverse events, zero other adverse events, and zero deaths in each safety group.