Comparison of Two Silicone Hydrogel Multifocal Contact Lenses: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Two Silicone Hydrogel Multifocal Contact Lenses (NCT04093258), a randomized na study. The primary outcome is Percentage of Participants With Lens Centration.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, crossover clinical trial comparing Dailies Total 1® Multifocal Contact Lenses with Air Optix® Multifocal Contact Lenses Plus HydraGlyde®. The registry lists an enrollment of 42 and a completed study. Participants were randomized to one of two sequences: Test/Control or Control/Test. In a crossover design, participants receive both treatments in sequence, allowing observations from the same participant under each treatment to contribute to comparison. The record does not explain how sequence, period, or within-participant correlation were handled in each analysis.

Participants were described as habitual soft contact lens wearers between 40-70 years old with presbyopia and hyperopia or myopia. The brief summary describes wearing the first lens for 8-12 days after a 7±3 day wash-out period, followed by repeating the procedures with the second lens. The arm descriptions instead state a 4-10 day washout period between fittings. Both descriptions are retained as recorded; the registry does not clarify their relationship. The primary outcome was assessed at 6 to 8 days, and the secondary outcome, Overall Handling Scores, was also assessed at 6 to 8 days.

The trial was single-masked, but the identity of the masked party is not reported in the registry record. The record identifies 42 participants enrolled, while the posted primary outcome group counts are 41 per lens and the secondary outcome group counts are 37 per lens. A participant flow account explaining the difference between enrollment and the outcome counts is not reported in the registry record. The original sample-size justification, planned analysis details, sequence allocation ratio, and handling of withdrawals 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: In total, 42 subjects were enrolled in this study; of which, 41 were randomly assigned into 2 sequences while, 1 subject failed to meet all eligibility criteria. Of the total assigned subjects, 40 subjects completed the study while, 1 subject was discontinued from the study.

Period 1

Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects dispensed at least one study lens.

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 Percentage of Participants With Lens Centration, measured over 6 to 8 days.

The primary endpoint was the percentage of participants with Grade 0 lens centration at 6 to 8 days. Lens position was assessed using a biomicroscope and graded on a scale from Grade 0 to Grade 2: Grade 0 represented centered, Grade 1 slightly decentered, and Grade 2 substantially decentered. The grades were then dichotomized, with Grade 0 counted as centered and Grade 1 or higher grouped as not centered. The reported percentage therefore concerns the share classified as centered, rather than the full distribution across all three grades.

Centration is a directly observed fitting characteristic of the study lenses. A binary endpoint can be straightforward to interpret as the proportion of participants meeting a defined classification. However, dichotomizing the grades discards information about the distinction between slight and substantial decentration. The endpoint also reflects assessment at a particular visit window; it does not describe how centration changes over longer use. The registry does not report further details about assessor training, repeat assessments, or reliability of the grading. The endpoint is therefore best read as a short-term, categorized lens-position measure, not as a complete account of lens performance or participant experience.

7. Results Posted in the Registry

• Test: 97.6% (40/41) versus 92.7% (38/41) on control; risk difference 4.9 percentage points (95% CI -4.4 to 14.1), risk ratio 1.05 (0.95–1.16); unadjusted two-proportion z-test p = 0.305.

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.

Overall Handling Scores

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test: mean 60.30 versus 55.30 on control; difference 5.00 (95% CI -3.60 to 13.60), standardized effect d = 0.27; z-test p = 0.254.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists Overall Handling Scores as the secondary outcome. It is a different type of measure from the primary lens-centration endpoint: it is reported as a mean score in CLUE points rather than a percentage classified as centered. The secondary outcome has fewer participants in each reported group than the primary outcome. The registry does not explain why the available outcome counts differ.

At the level of broad pattern, the secondary findings do not supply a precise, independent confirmation of the primary comparison. They address handling rather than centration, and their interpretation depends on a different measurement scale and analysis. The posted secondary analysis is labeled non-inferiority, but its margin and detailed decision criteria are not reported in the registry record. It is therefore important not to infer a conclusion about the secondary outcome from its analysis label alone.

Secondary outcomes are often useful for describing other dimensions of a trial, but they generally carry less evidential weight than the prespecified primary outcome when many comparisons or outcomes are considered. Testing multiple outcomes can increase the chance of at least one apparently notable result by chance. An adjustment for multiplicity, a hierarchy for interpreting outcomes, or a prespecified testing strategy is not reported in the registry record. The secondary result should therefore be treated as supportive descriptive information, not as a standalone basis for a broad claim or as a substitute for the primary endpoint.

The record lists one secondary outcome, but also states that three outcome measures and three analyses were posted. The relationship among those counts and any additional outcome-level details is not explained in the registry record. A complete endpoint inventory and analysis plan would help readers assess selective reporting and the role assigned to each result. Without that information, the secondary outcome is best interpreted cautiously and alongside the primary result, not as a separate definitive test.

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

• Overall Handling Scores

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary: each participant's lens assessment was classified as centered or not centered. For a binary outcome, the percentage is the share of participants in a group who met the specified classification. Here, centered means Grade 0; Grades 1 and 2 were combined as not centered. The reported group percentages can be read as observed proportions in the outcome population, rather than as measurements of the degree of decentration.

What does the risk difference represent?

The unadjusted recalculation expresses the contrast as a risk difference, which subtracts the Control proportion from the Test proportion on the probability scale. Its estimate is 0.049, and its confidence interval extends from -0.044 to 0.141. A value of zero corresponds to equal proportions in the two groups. Values on either side of zero represent differences in opposite directions. Because the interval includes zero, the data are compatible with no difference as well as with differences in either direction within the interval. This is a general explanation of how to read an interval; it does not turn the estimate into an adjusted crossover analysis.

How does the reported odds ratio differ?

An odds ratio compares the odds of the binary outcome between groups rather than comparing the proportions directly. Odds and proportions are related but are not the same scale. The sponsor's reported analysis uses a generalized linear mixed model and gives an odds ratio of 1.51, with a 95% confidence interval from 0.33 to 6.85. A mixed model can account for structured observations, such as repeated measurements or grouping, if the model is specified to do so. The registry does not describe the model terms, covariance structure, or how sequence and period were represented. Those details cannot be inferred from the method label alone.

In a crossover trial, each participant experiences both lenses. Measurements from a participant are therefore related rather than independent in the way measurements from unrelated people would be. General statistical methods for crossover data account for this dependence and may also consider period or sequence. The posted sponsor method is described as a generalized linear mixed model, but the registry record does not provide enough specification to judge which crossover features were included. The recalculated risk difference is explicitly an unadjusted comparison from posted summary counts; it should not be mistaken for a model-based estimate that accounts for within-participant data.

What does the non-inferiority label mean?

Non-inferiority is a design and inference framework that asks whether an intervention is not worse than a comparator by more than a prespecified margin. The margin defines the largest difference that would still meet the study's criterion. The registry labels the sponsor analysis as non-inferiority, but does not report the margin, the direction of the criterion, or the detailed decision rule. It also reports no p-value for that analysis. Without those elements, the label describes the analysis type recorded, but the posted result cannot independently show whether the study met a non-inferiority criterion.

Generalized linear mixed models can be useful for binary outcomes and correlated observations. Their estimates depend on model specification, including the link function, random or repeated effects, and covariates. Those specifications are not reported in the registry record. The outcome data also have high observed percentages in both groups, a setting where odds ratios may be less intuitive than direct proportions. The odds ratio and the observed percentages answer related but distinct statistical questions, and their numerical values should not be compared as if they were on the same scale.

What does an unadjusted p-value tell the reader?

The unadjusted p-value of 0.305 belongs to the recalculated summary-data comparison. In general, a p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. Here, the recalculation is not reported as the trial's sponsor model and does not incorporate crossover-level information unavailable in the group summaries. It should therefore be interpreted as a simple unadjusted comparison, not as a replacement for the sponsor's analysis.

Confidence intervals add information about precision by giving a range of estimates compatible with the analysis and its assumptions. A wide range indicates that the data do not tightly determine the underlying contrast. The primary risk-difference interval includes both zero and values on either side, while the model-based odds-ratio interval is broad. The two intervals arise from different measures and methods, and they should not be combined or treated as duplicate estimates. Neither interval removes uncertainty about unreported design and analysis details.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is 0.049, with a confidence interval from -0.044 to 0.141. The interval includes zero and extends to estimates favoring either group, so the direction and size of the underlying difference are not sharply determined by these summary data. The interval also spans differences that may be meaningful or not, depending on a clinical threshold; such a threshold is not reported in the registry record.

The sponsor's model-based odds ratio is 1.51, with a 95% confidence interval from 0.33 to 6.85. This is a wide interval, indicating considerable uncertainty on the odds-ratio scale. It includes values on both sides of 1, the value corresponding to equal odds. The model estimate and the unadjusted risk difference use different scales and methods, so their intervals should be interpreted separately.

In general, a confidence interval reflects the range of estimates compatible with the observed data under the statistical model and its assumptions. It does not guarantee that the true value lies in the interval, and it does not account for weaknesses or missing details in the analysis. The registry does not report the original sample-size justification or the planned precision target. It is therefore not possible to determine whether the trial was designed to estimate the difference with a particular degree of precision. The outcome counts and intervals are more informative for uncertainty than a simple statement that a comparison did or did not cross a significance threshold.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. For this non-time-to-event outcome, the figures are participants per arm, not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect. The trial's own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the listed assumptions, if that effect is the true one and the statistical model assumptions hold. The 90% power column gives the corresponding planning figure for a 90% chance. These are planning targets, not observed power for this completed trial. The figures are not a retrospective score of how well the trial performed.

The rows distinguish planning for 100%, 75%, and 50% of the observed effect. Smaller target effects require more participants per arm because a smaller difference is harder to distinguish from sampling variation. The figures should be treated as illustrations rather than a substitute for a prospective design calculation. A future design would need a clinically justified effect, a suitable analysis plan for the crossover structure or any alternative design, and clearly specified assumptions. The registry does not report those original planning choices, so the displayed planning calculations cannot be taken as evidence about the rationale for the enrollment target in this trial.

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 = 0.927; treatment proportion p₁ = 0.976; average p̄ = 0.951.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3046 = 0.5971.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3027 = 0.2547.
4. n = (0.5971 + 0.2547)² / (0.0488)² = 304.9, rounded up to 305 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 <- 0.926829268292683                          # control proportion
p1 <- 0.975609756097561                          # 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(4093258)
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 = 305 (80% power), 408 (90% power)
 75% of observed effect: n per arm = 608 (80% power), 813 (90% power)
 50% of observed effect: n per arm = 1,510 (80% power), 2,021 (90% power)
power.prop.test: 304.9 
Simulated power at n = 305 per arm: 0.823 (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. Analyses Reported by the Sponsor

The sponsor's reported primary analysis is a generalized linear mixed model analysis of odds, with an odds ratio of 1.51 and a 95% confidence interval from 0.33 to 6.85. It is labeled as a non-inferiority analysis. The sponsor analysis is the trial's reported model-based result and should be distinguished from the unadjusted recalculation based on the posted group counts.

The recalculation expresses the comparison as a risk difference of 0.049, with a confidence interval from -0.044 to 0.141 and an unadjusted p-value of 0.305. It is based on the summary counts and does not model the crossover structure. The two analyses therefore differ in both effect measure and statistical approach; they are not competing calculations of precisely the same quantity under identical assumptions.

The registry does not report the sponsor model's detailed specification, the non-inferiority margin, or a p-value for the sponsor analysis. Consequently, the reported odds ratio and interval can be described, but a non-inferiority decision cannot be reconstructed from the information recorded. The recalculation offers a transparent, simple comparison of the posted proportions, while the sponsor analysis remains the registry's own reported analysis. Neither result removes the uncertainty reflected in the intervals.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when more than one outcome, time point, subgroup, or analysis is examined. In general, making several statistical comparisons without an adjustment or prespecified hierarchy increases the possibility that one comparison will appear notable by chance. This trial lists the primary lens-centration outcome and Overall Handling Scores as a secondary outcome. The registry does not report a multiplicity adjustment, a hierarchy of hypotheses, or a plan specifying how the secondary result should affect interpretation of the primary result.

The record states that three outcome measures and three analyses were posted, while naming one secondary outcome in addition to the primary endpoint. It does not explain how the outcome and analysis counts correspond. Nor does it provide enough information to establish whether there were additional time points, analysis populations, or other planned comparisons. These matters are not reported in the registry record and should not be inferred from the posted summary alone.

Missing-data and participant-flow details are also limited. The registry records enrollment of 42, gives 41 participants per group for the primary outcome, and 37 per group for Overall Handling Scores. It does not report the reasons for these differing counts, whether missing observations were excluded or imputed, or how missingness was handled in the sponsor models. The outcome population is described as all subjects dispensed at least one study lens, but further analysis-population definitions are not reported.

Because this is a crossover study, a full analysis plan would also be useful for understanding how participants who did not complete both periods were handled, whether sequence and period effects were considered, and how within-participant correlation was modeled. Those details are not reported in the registry record. These omissions do not invalidate the posted summaries, but they limit how completely readers can assess the analyses and the risk of selective or incomplete reporting.

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 posted serious adverse event figures show 0 serious adverse events among 41 participants at risk in the Test group and 0 among 41 participants at risk in the Control group. The record also lists 0 other adverse events and 0 deaths in each group. These are the counts recorded for the trial and should be read as event counts, not as proof that no adverse events could occur.

Zero observed events in these groups provides limited information about uncommon events, particularly in a trial with a small number of participants and short outcome windows. The registry does not provide further details on adverse-event collection procedures, definitions, severity grading, or follow-up completeness. It also does not list any serious adverse event terms. The figures describe what was reported, but do not establish comparative safety beyond the trial's recorded observation.

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

The result describes short-term lens centration in participants who were habitual soft contact lens wearers with presbyopia and hyperopia or myopia. At 6 to 8 days, the posted percentages classified most assessed lenses as centered in both groups. The unadjusted recalculation estimates a risk difference of 0.049, but its confidence interval includes zero and is broad enough to encompass estimates in either direction. This is a description of the posted results, not a claim that one lens is better or worse.

The sponsor's analysis is labeled non-inferiority, but the registry record does not report the margin that defines how much difference would be acceptable, or a p-value for that model. A non-inferiority conclusion therefore cannot be independently determined from the information recorded. Likewise, the results do not establish equivalence: absence of a statistically clear difference is not evidence that two treatments are exactly the same.

The endpoint concerns a categorized assessment of lens position at a specific visit window. It does not represent all aspects of comfort, vision, ease of use, longer-term performance, or safety. The secondary handling score concerns another dimension, but its interpretation is also limited by the missing non-inferiority details and analysis-plan information. The registry does not report follow-up beyond the short wearing periods described.

The findings apply to the study population and procedures recorded in this trial. They should not automatically be generalized to people who differ from the eligible participants, other lens types, or use conditions not represented in the record. Statistical uncertainty, missing analysis details, and differing group counts all matter when interpreting the result. The numbers are evidence about the assessments recorded in this trial, not individual treatment guidance.

18. Why This Trial Matters Statistically

This trial illustrates how the statistical interpretation of a clinical comparison depends on the outcome definition, design, and analysis—not only on the group percentages. The primary endpoint converts a three-grade assessment into a binary classification. That makes the result easy to express as the proportion centered, but it also removes distinctions between slightly and substantially decentered lenses.

The crossover design is another important feature. Each participant received both lenses in sequence, which creates paired observations. A summary comparison of group percentages does not retain the pairing, while a mixed model may account for structured repeated observations if appropriately specified. The registry gives the sponsor method label and model estimate but not enough details to assess the implementation. This makes the contrast between the transparent unadjusted recalculation and the reported model especially instructive.

The record also demonstrates why a non-inferiority label is not sufficient on its own. Interpreting non-inferiority requires the margin and the decision criteria, neither of which is reported. In addition, confidence intervals convey how much uncertainty remains: the primary unadjusted interval includes zero and covers a range of possible effects. A point estimate alone would hide that uncertainty.

Finally, outcome counts, missing-data explanations, and multiplicity plans are part of statistical interpretation. Enrollment and analysis counts differ, and the registry does not explain those differences. These details matter to readers assessing the completeness, precision, and scope of evidence. The trial is a useful example of why careful reading combines the numerical estimates with study design and reporting context.

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

Several trial-specific limitations constrain interpretation. The registry describes a crossover design but does not report sufficient detail about how the sponsor's model handled participant pairing, period effects, sequence effects, or within-participant correlation. The unadjusted recalculation uses group summary counts and does not account for those features.

The primary outcome combines Grade 1 and Grade 2 into one category, so the posted percentage does not show how many assessments were slightly versus substantially decentered. The record does not provide the grade-specific counts or details about assessor training, masking of the assessor, or repeatability of the biomicroscope assessment. Although the study is described as single-masked, the masked party is not identified.

The primary group counts are 41 per lens, while the secondary group counts are 37 per lens, compared with 42 enrolled. Reasons for these differences and missing-data handling are not reported. The brief summary describes a 7±3 day wash-out period, while the arm descriptions specify 4-10 days; the registry does not explain the relationship between these descriptions.

The sponsor's primary and secondary analyses are labeled non-inferiority, but the margins, full statistical plans, and p-values are not reported. The original sample-size justification and multiplicity strategy are also not reported. Finally, the observed outcome assessments cover 6 to 8 days, and the record does not provide evidence about longer-term outcomes. These limits make the results most informative as short-term summaries of the recorded measures in this study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparison of Two Silicone Hydrogel Multifocal Contact Lenses — NCT04093258.
• Registry record last updated 2021-12-01; status last verified 2021-11.
• Results first posted 2021-02-16.
• 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

NCT04093258 was a completed, randomized, single-masked crossover trial comparing Dailies Total 1® Multifocal Contact Lenses with Air Optix® Multifocal Contact Lenses Plus HydraGlyde®. It enrolled 42 participants who were described as habitual soft contact lens wearers between 40-70 years old, with presbyopia and hyperopia or myopia.

The primary endpoint was the percentage classified as having Grade 0, centered lens position, assessed at 6 to 8 days. The posted percentages were 97.3 for Test and 91.9 for Control, with 41 participants in each group. The sponsor reported a generalized linear mixed model odds ratio of 1.51, with a 95% confidence interval from 0.33 to 6.85, labeled as non-inferiority. The non-inferiority margin is not reported in the registry record.

Overall Handling Scores was the listed secondary outcome. The record does not explain the differences in outcome counts or provide full analysis, missing-data, multiplicity, and sample-size planning details. The results should therefore be interpreted as short-term posted findings with substantial uncertainty and important design details unreported.