Clinical Evaluation of Opti-Free III (FID 109182) Compared to Opti-Free Plus® in Japan: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Evaluation of Opti-Free III (FID 109182) Compared to Opti-Free Plus® in Japan (NCT02251561), a randomized na study. The primary outcome is Proportion of Participants Scoring ≥ 2 for Corneal Staining Density With Fluorescein.

2. Clinical Question

The core question is about a short-term examination finding under the study conditions, not about longer-term contact lens experience or outcomes beyond corneal staining. The record describes random assignment of which eye received the FID 109182 lens, with the other product used in the fellow eye. This contralateral arrangement lets the two products be assessed within the same participant, while the registry’s posted summaries report results by product. The statistical method used to account for the within-participant pairing is not reported in the registry record.

3. Trial Design

The registry describes a randomized, double-masked study with a single-group model. It lists an enrollment of 36 and a status of completed. The study began in 2013-11, and primary completion was in 2014-05. The phase is listed as NA. Alcon Research is named as the sponsor.

The brief description says the study compared the investigational contact lens care product FID 109182 with Opti-Free Plus when used with Acuvue Oasys contact lenses. The intervention and arm descriptions identify Senofilcon A lenses. Lenses were pre-soaked in their assigned product for 24-48 hours before a 2-hour contralateral wear period. The eye assigned to FID 109182 was randomized to the right or left eye; the Opti-Free Plus lens was worn in the fellow eye. Thus, the design uses two eyes within a participant rather than describing two separate parallel groups of people.

For the primary endpoint, the registry posts an analysis population of 27 for each product. The safety record lists 28 at risk for each product. These are the reported figures for their respective analyses; the registry does not explain why the analysis populations differ or how missing examination data were handled. The enrollment figure should not be read as the number included in each posted endpoint analysis.

Randomization and masking are design features, but the registry does not report the randomization sequence method, who was masked, how masking was maintained, or the method used to analyze the paired eye measurements. It also does not report the original sample-size assumptions or a detailed statistical analysis plan. Those omissions limit assessment of how closely the posted analysis followed the intended design.

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 36 subjects enrolled in the study, 8 were exited prior to product exposure \[did not meet eligibility criteria (5), and subject withdrawal (3)\]. This reporting group includes all subjects who used the study products (28).

Overall Study

Analysis population for the primary outcome, as defined in the registry: This analysis population includes all subjects who used the study products and had examination/observation data after use.

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: This analysis population includes all subjects who used the study products.

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Participants Scoring ≥ 2 for Corneal Staining Density With Fluorescein, measured over Day 1, after 2 hours of wear.

The primary endpoint is the proportion of participants scoring at least 2 for corneal staining density with fluorescein at Day 1, after 2 hours of wear. After lens removal, the cornea was stained with fluorescein and pictures of the corneal surface were taken. Staining density was evaluated for each eye individually against representative pictures, using a scale from 0 to 3: no staining, low-density staining, moderate-density staining, and severe staining.

The endpoint combines scores of 2 and 3 into the event of interest. It therefore records whether staining density reached at least the moderate category, rather than preserving all distinctions across the scoring scale. The registry reports the result as a percentage of participants. For the primary endpoint, 92.6% of the FID 109182 group and 22.2% of the Opti-Free Plus group met that threshold.

As a general statistical point, a binary proportion can make a clinically defined threshold easy to interpret, but it loses information about differences among scores within the event and non-event categories. The endpoint is useful for comparing the frequency of reaching the stated threshold under the study conditions. It does not, by itself, describe the full distribution of staining scores, the duration of any finding, or outcomes beyond the examination after the short wear period.

7. Results Posted in the Registry

• Opti-Free Plus: 22.2% (6/27) versus 92.6% (25/27) on control; risk difference -70.4 percentage points (95% CI -88.9 to -51.8), risk ratio 0.24 (0.12–0.49); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Proportion of Participants Scoring ≥ 2 for Corneal Staining Area With Fluorescein

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Opti-Free Plus: 44.4% (12/27) versus 92.6% (25/27) on control; risk difference -48.1 percentage points (95% CI -69.3 to -27.0), risk ratio 0.48 (0.31–0.74); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Opti-Free Plus than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary endpoint assesses the proportion scoring at least 2 for corneal staining area with fluorescein at Day 1, after 2 hours of wear. Its overall pattern is similar to the primary endpoint: the proportion reaching the stated threshold is higher for FID 109182 than for Opti-Free Plus, and the registry reports an unadjusted p-value of <0.001 for the comparison.

The two outcomes are related in that both concern fluorescein staining assessed after the same wear period, and both use a threshold of at least 2. They measure different features, however: the primary outcome is staining density, whereas the secondary outcome is staining area. Agreement in direction across these measures adds descriptive consistency to the posted results, but it does not make them duplicate measurements or establish that one outcome confirms the other under a prespecified testing strategy.

The registry does not report a multiplicity adjustment, a hierarchy of outcomes, or a plan for interpreting multiple tests. As a general statistical point, when several outcomes are tested, the chance of at least one apparently strong result can increase unless the testing strategy accounts for multiplicity. An unadjusted secondary result therefore carries less confirmatory weight than a result interpreted under a prespecified, adequately documented plan. The registry also lists no reported analyses, so details of formal testing are not available beyond the posted comparison summaries.

The secondary endpoint should be read as supportive descriptive evidence about a distinct staining characteristic, not as a substitute for the primary endpoint or evidence about outcomes beyond those recorded. The record does not establish whether the secondary measure was prespecified, how missing data were treated, or whether the grader assessments were analyzed with the paired-eye design in mind. Those uncertainties limit how strongly the secondary result can reinforce the primary result.

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

• Proportion of Participants Scoring ≥ 2 for Corneal Staining Area With Fluorescein

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary for analysis: each participant is classified according to whether the corneal staining density score reached at least 2. The registry reports the percentage meeting that threshold for each product and a risk difference comparing Opti-Free Plus with FID 109182. The arm percentages are 92.6% and 22.2%, respectively. The posted risk difference is -0.704, and the registry reports an unadjusted p-value of <0.001.

What does a risk difference describe?

As a general statistical explanation, a risk difference subtracts one event proportion from another, with the sign depending on the stated comparison order. It is an absolute measure on the probability scale: it describes how far apart the proportions are, rather than expressing one proportion as a multiple of the other. Here, the comparison is stated as Opti-Free Plus relative to FID 109182. The negative estimate indicates a lower observed event proportion in the Opti-Free Plus group. The posted estimate should be interpreted with its confidence interval and with attention to how the two eyes from each participant were handled.

Why does the paired-eye design matter?

The trial used one eye for each product within a participant. As a general statistical point, measurements from two eyes in the same person may be related because both eyes share characteristics of that person. An analysis that treats the eye-level results as independent may not reflect that dependence; a paired analysis can use the within-person comparison. The registry does not report whether the primary comparison used a paired method, how discordant eye results were handled, or which test produced the posted p-value. Accordingly, the displayed comparison can be described, but its exact statistical implementation cannot be independently assessed from the registry record.

How should the p-value be read?

In general, a p-value is calculated under a specified null model and test procedure. It summarizes how incompatible the observed data are with that model; it is not a measure of the probability that a result is due to chance, nor is it a measure of treatment benefit. The reported unadjusted p-value is <0.001. Because the test procedure and its assumptions are not reported, the number can be quoted as posted but the precise inferential calculation cannot be reconstructed from the registry record. The word unadjusted also matters: the record does not state that this result accounts for the fact that more than one outcome was reported.

What does a confidence interval add?

As a general explanation, a confidence interval describes a range of effect values compatible with the observed data under a stated method and its assumptions. It conveys uncertainty about the estimate, while a single estimate alone does not. The registry gives a confidence interval for the risk difference, but it does not report the interval method. Its interpretation also depends on the analysis properly reflecting the trial’s paired-eye structure. The interval does not capture every source of uncertainty, such as selective reporting or departures from the analysis assumptions.

What can be inferred from the analysis population?

The primary endpoint description says the analysis includes subjects who used the study products and had examination or observation data after use. The posted primary outcome lists 27 for each product. The record does not explain exclusions, missing eye assessments, or whether all randomized participants were included. As a general principle, excluding observations with missing outcome data can affect an estimate if the likelihood of missingness is related to the outcome or assigned product. The registry does not give enough information to assess whether that concern applies.

The registry reports no analysis method, covariate adjustment, sensitivity analysis, interim analysis, or detailed statistical analysis plan. These items are not reported in the registry record. No adjusted result should be inferred from the unadjusted comparison. In general, adjustment may be used for prespecified factors or design features, but whether and how it was used in this trial is not documented. The same caution applies to the choice of threshold, scoring procedures, and whether graders remained masked.

The primary and secondary outcomes are both expressed as percentages meeting a threshold. The primary measure concerns staining density; the secondary measure concerns staining area. Although both are binary proportions, they represent different features of the corneal images and should not be treated as interchangeable. The record’s comparison estimates can describe each outcome separately. Without a reported analysis plan or multiplicity procedure, the strength of evidence across outcomes requires caution.

11. Confidence Intervals and Precision

The registry reports a confidence interval for the primary risk difference. A confidence interval is, in general, a range of values that are compatible with the observed data under the interval’s statistical method and assumptions. It helps show the uncertainty around the point estimate; it is not a guarantee that the true value lies in the interval, nor does it account automatically for design or reporting limitations.

The primary comparison’s interval lies below zero, consistent with the negative risk-difference estimate and the lower observed event proportion for Opti-Free Plus. Its width indicates that there remains uncertainty about the size of the contrast, even though the reported unadjusted p-value is <0.001. The interval endpoints are not repeated because the registry reports them at a precision that cannot be quoted under the number-format limit. The estimate and interval are on the risk-difference scale, not a ratio scale.

Precision should be considered in light of the endpoint analysis population, which lists 27 for each product, and the paired-eye design. The registry does not identify the confidence-interval method or say whether within-participant dependence was incorporated. If the method did not reflect pairing, the stated interval could misrepresent uncertainty; the available record does not permit a determination either way.

The confidence interval addresses sampling uncertainty under its method, not uncertainty from missing data, measurement variation, selective outcome reporting, or limited generalizability. The observed percentages are specific to the registry’s stated population and examination after 2 hours of wear. Precision in this short-term comparison should not be confused with precision about outcomes under longer-term or different use conditions.

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 registry’s sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. They are reported as participants per arm, not as total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario targets a stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the effect used in that scenario, if the assumptions and effect are correct. The 90% power column uses a higher target chance of detection under the same general framework. These are planning concepts, not guarantees for a future study, and the calculations rely on the assumptions listed in the record.

For the primary outcome, the illustration using 100% of the observed effect gives 7 participants per arm for 80% power and 9 participants per arm for 90% power. Planning for 75% of the observed effect gives 12 participants per arm for 80% power and 15 participants per arm for 90% power. Planning for 50% gives 23 participants per arm for 80% power and 30 participants per arm for 90% power. Smaller effects require more participants because they are harder to distinguish from random variation.

These figures are not observed power. They do not show the probability that the completed trial detected an effect, and they should not be used to explain the trial’s results after the fact. They are illustrations of how sample size changes when the target effect and power target change, under the stated planning assumptions. The registry does not report whether the original study was designed using these assumptions.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.926; treatment proportion p₁ = 0.222; average p̄ = 0.574.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6993 = 1.3706.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4914 = 0.4135.
4. n = (1.3706 + 0.4135)² / (-0.7037)² = 6.4, rounded up to 7 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
p0 <- 0.925925925925926                          # control proportion
p1 <- 0.222222222222222                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2251561)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 7 (80% power), 9 (90% power)
 75% of observed effect: n per arm = 12 (80% power), 15 (90% power)
 50% of observed effect: n per arm = 23 (80% power), 30 (90% power)
power.prop.test: 6.4 
Simulated power at n = 7 per arm: 0.863 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome for staining density and a secondary outcome for staining area. It reports comparison summaries for both, but does not report a multiplicity adjustment, a gatekeeping procedure, or a hierarchy specifying how the outcomes were to be tested. The reported p-values are unadjusted. Whether any multiplicity plan was specified outside the registry record is not reported in the registry record.

As a general statistical explanation, multiplicity arises when more than one hypothesis is evaluated. Without an appropriate prespecified strategy, interpreting each unadjusted p-value as if it were the only test can overstate the overall strength of evidence. This does not mean that the posted results are invalid; it means that the record does not establish how the family of outcomes was handled. The secondary result is therefore best treated as supportive rather than as an independent confirmatory finding.

The primary analysis population is described as subjects who used the products and had examination or observation data after use. The primary outcome reports 27 for each product, while the safety figures list 28 at risk for each product. The reason for that difference is not reported in the registry record. It is also not reported how many assessments were missing, whether any participants were excluded after randomization, or how incomplete observations were handled.

As a general matter, missing-data methods can affect results when the probability of a missing measurement relates to the outcome or study condition. The registry does not report a missing-data strategy or sensitivity analysis, so the impact of missingness cannot be assessed. The precise definition of the analysis population beyond the stated use and observation criteria is not reported in the registry record.

The record lists randomized allocation and double masking, but does not report the randomization procedure, masking roles, or safeguards against unmasking. It does not give a statistical analysis plan, test method, paired-eye model, or interim-analysis information. Those details are not reported in the registry record. Consequently, the results can be described using the posted summaries, but assessment of prespecification, analysis fidelity, and robustness is limited.

15. Safety Results

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

Other (non-serious) adverse events

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

The registry’s safety figures list 28 participants at risk for serious adverse events in each product group, with zero serious adverse events reported in either group. It also lists zero other adverse events in each group. These counts describe the safety information posted for the registry record and should be read in relation to the stated at-risk figures.

A count of zero reported events does not establish that an event is impossible or that the products have no safety risks. As a general statistical point, an event may not be observed in a study even when its underlying occurrence is possible, particularly when the safety observation period or population is limited. The record concerns a short wear period, and it does not provide further detail on the safety surveillance window, event definitions, or methods for soliciting and adjudicating events.

The death figures are not reported in the registry record. The listed adverse-event information does not provide detail about event severity beyond the serious-event classification, timing, relatedness assessments, or reasons for any missing safety data. It should not be interpreted as a comprehensive safety profile or as evidence about longer-term use.

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

The posted results describe corneal staining after a specific short-term study procedure: lenses were pre-soaked in the products for 24-48 hours, worn for 2 hours, removed, and assessed with fluorescein on Day 1. For staining density, the proportion reaching a score of at least 2 was 92.6% for FID 109182 and 22.2% for Opti-Free Plus. The secondary staining-area outcome follows the same general direction, with a higher threshold-event proportion for FID 109182.

These observations do not establish a general conclusion about either product’s performance or safety. The record does not cover longer wear, repeated use, other lens types, or outcomes beyond the recorded staining measures. It also does not report enough detail about the statistical analysis to verify whether the within-participant, paired-eye structure was incorporated or how missing outcome data were handled.

The result does not describe the full distribution of staining scores. The primary endpoint combines scores of 2 and 3, so it cannot distinguish moderate from severe staining in the reported proportion. Nor does the endpoint state how long an observed staining score persisted or what it means for outcomes not measured in the trial.

The unadjusted p-value indicates a strong statistical contrast under the test assumptions, but statistical evidence is not the same as clinical importance, and a p-value is not the probability that the null hypothesis is true. The confidence interval provides information about precision under its method, but the registry does not report the method or its treatment of paired eyes. Interpretation therefore rests on the posted observations while retaining caution about undocumented analysis choices and generalizability.

The registry record is a source of trial-specific results, not individualized medical guidance. Its findings should be understood within the population, procedures, endpoints, and limitations recorded for this study.

17. Why This Trial Matters Statistically

This trial is statistically notable because it measures both eyes of a participant under different product conditions. That contralateral arrangement can control some sources of person-to-person variation, but it also means the eye-level observations are linked within each participant. The registry reports a randomized eye assignment and product-specific outcome summaries, yet does not report whether the comparison method accounted for that pairing. Recognizing the relationship between design and analysis is essential when interpreting an estimate and its uncertainty.

The primary result also illustrates how endpoint definition shapes interpretation. Converting an ordinal staining grade into a binary event at a threshold can make a proportion straightforward to communicate, but it discards distinctions within the score categories. The posted percentages answer a specific threshold question, not every question about the distribution or severity of staining.

Another important issue is the distinction between a striking observed contrast and the strength of confirmatory evidence. The registry reports an unadjusted p-value and a secondary endpoint in the same direction, but does not document a multiplicity strategy or detailed analysis plan. Consistency across outcomes is informative descriptively, while undocumented testing choices limit formal confirmation.

Finally, planning calculations based on the observed effect should not be mistaken for the study’s original sample-size justification or for observed power. The registry provides planning illustrations, but the original design assumptions are not reported. Together, these features make the record useful for understanding effect estimates, endpoint construction, dependence between measurements, and the limits of registry-level statistical detail.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary analysis population is smaller than the enrollment figure, and the safety at-risk figures differ from the primary endpoint population figures. The registry does not explain these differences, identify exclusions, or describe missing observations. This prevents a complete accounting of the participants contributing to each outcome and limits evaluation of possible selection effects.

The design compares products between fellow eyes, but the statistical method for the within-participant comparison is not reported. The confidence-interval method and test procedure are also not reported. Without those details, it is not possible to verify whether the posted uncertainty estimates reflect the paired structure or to reproduce the inferential analysis.

The study evaluates an examination finding after 2 hours of wear on Day 1, following pre-soaking for 24-48 hours. This short, specific procedure limits the scope of the results. The registry does not report repeated-use findings, longer-term outcomes, or other clinical measures. The primary threshold also combines moderate and severe density scores, leaving the underlying score distribution unclear.

The record does not report the original sample-size justification, detailed analysis plan, multiplicity procedure, interim analyses, randomization implementation, masking roles, or grader reliability. It also does not explain whether endpoint thresholds were selected before data review. These omissions do not erase the posted outcome summaries, but they restrict assessment of prespecification, measurement reliability, and the robustness of the comparisons.

The safety record gives event counts but not detailed surveillance methods, event timing, relatedness, or the safety observation window. Death counts are not reported in the registry record. The findings therefore provide limited information about safety beyond the events listed for the recorded study period.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Evaluation of Opti-Free III (FID 109182) Compared to Opti-Free Plus® in Japan — NCT02251561.
• Registry record last updated 2015-06-10; status last verified 2015-06.
• Results first posted 2015-06-10.
• 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

NCT02251561 is a completed randomized, double-masked study comparing FID 109182 with Opti-Free Plus for corneal staining when used with Senofilcon A contact lenses. The registry describes pre-soaking for 24-48 hours and a 2-hour contralateral wear period. Primary completion was in 2014-05.

The primary endpoint was the proportion scoring at least 2 for corneal staining density with fluorescein on Day 1, after 2 hours of wear. The posted proportions were 92.6% for FID 109182 and 22.2% for Opti-Free Plus; the reported unadjusted p-value was <0.001. The secondary endpoint assessed staining area and had the same overall direction.

The registry reports product-specific endpoint summaries and safety counts, but does not provide a detailed statistical analysis plan, paired-eye method, missing-data strategy, or multiplicity procedure. Results should be interpreted within the study’s short-term conditions and the limits of the information reported in the registry record.