Clareon Toric vs Eyhance Toric: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clareon Toric vs Eyhance Toric (NCT05481125), a randomized na study. The primary outcome is Mean Binocular Best-corrected Distance Visual Acuity (BCDVA) at 4 Meters Under Bright Lighting Conditions.

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel-group trial sponsored by Alcon Research. The registry lists the study as completed. The study start date was 2022-10-10, and the primary completion date was 2023-10-16. Phase is recorded as not applicable.

The two groups differed by the intraocular lens family used following phacoemulsification surgery. Clareon/Clareon Toric participants received an Alcon Clareon lens or Clareon Toric lens as indicated. Eyhance/Eyhance Toric participants received a TECNIS Eyhance lens or TECNIS Eyhance Toric II lens as indicated. In both groups, second-eye surgery was recommended within 14 days after the first-eye operation. The registry describes the study as double-masked but does not report which participants or study personnel were masked, or how masking was maintained.

Total enrollment is listed as 203. The primary outcome results are reported for participants with visit data: 86 in the Clareon group and 81 in the Eyhance group. The registry does not explain the difference between overall enrollment and the outcome denominators, or report the handling of participants without a recorded visit result.

The study’s primary purpose was to compare binocular best-corrected distance visual acuity at 3 months postoperative. The posted outcome is the mean at the month 3 postoperative visit. The registry record does not report the original sample-size justification, the planned allocation ratio, the randomization method, or detailed analysis procedures. Those details should not be inferred from the observed group counts or from planning illustrations based on the observed result.

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 203 enrolled, 14 subjects were exited prior to randomization as screen failures, and 14 subjects were discontinued after randomization and prior to attempted implantation. This reporting group includes all subjects with attempted implantation per actual treatment (175).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: AAS with data at visit

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 Implanted Analysis Set (AAS): All eyes with successful study IOL implantation and with at least one postoperative visit.

6. Primary Endpoint

The registry lists the primary outcome as Mean Binocular Best-corrected Distance Visual Acuity (BCDVA) at 4 Meters Under Bright Lighting Conditions, measured over Month 3 postoperative visit.

The primary endpoint is mean binocular best-corrected distance visual acuity (BCDVA) at 4 meters under bright lighting conditions at the month 3 postoperative visit. Visual acuity was tested with a refraction chart using the correction obtained from a manifest refraction. The measurement is expressed in logMAR units. The registry notes that 0.00 logMAR corresponds to 20/20 Snellen acuity, described as normal distance eyesight, and that lower or more negative logMAR values indicate better measured acuity.

The endpoint is subject-based: each participant receives one score representing both eyes. This is distinct from treating each eye as an independent observation. A binocular measure is relevant to the stated study question because the comparison concerns visual acuity using both eyes together at the follow-up visit. The mean summarizes the group’s average observed score; it does not describe every participant’s result or the full distribution of scores.

The registry’s brief summary describes the comparison as occurring at 3 months postoperative, consistent with the posted month 3 timeframe. The record does not report a clinically important difference threshold for this measure. Therefore, the statistical contrast alone cannot establish how the observed difference should be interpreted in terms of clinical importance.

7. Results Posted in the Registry

• Eyhance/Eyhance Toric: mean -0.06 versus -0.10 on control; difference 0.05 (95% CI 0.02 to 0.07), standardized effect d = 0.56; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean difference represent?

For a continuous outcome such as logMAR acuity, a mean difference compares the average values in two groups. The recalculated contrast is expressed as the Eyhance-family group mean minus the Clareon-family group mean. A positive value in that direction means the average logMAR value was higher in the Eyhance group. Since lower logMAR indicates better measured acuity, the direction of the numerical scale matters when describing the result. A mean difference is an average contrast; it does not imply that each participant experienced the same value or difference.

The two posted means are -0.1 and -0.055 logMAR. The recalculated unadjusted difference is 0.045 logMAR. This calculation is based on group-level summaries, not participant-level data. It does not account for possible covariates, departures from the analysis population, or other modeling choices. The registry does not report whether the sponsor’s analysis incorporated such adjustments.

What does the standard deviation describe?

A standard deviation describes the spread of individual observations around a group mean. It is not the uncertainty in the mean itself: the standard error describes the sampling uncertainty of an estimated mean, and a confidence interval combines that uncertainty with a chosen confidence level. The posted outcome lists standard deviations for the groups, but the registry record does not provide confidence limits for each group mean.

What does the confidence interval communicate?

General statistical explanation: a confidence interval gives a range of values that are compatible with the observed data and the assumptions of the method used to calculate it. It is not a guarantee that the true effect lies in the particular interval, nor does it express the probability that a treatment effect is clinically important. The recalculated interval for the mean difference excludes zero. That finding is consistent with the small unadjusted p-value, but the interval and p-value do not establish clinical relevance. No clinical importance threshold is reported in the registry record.

The registry’s sponsor analysis is labelled non-inferiority. General statistical explanation: a non-inferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified margin. The margin and the method used to evaluate it are not reported in the registry record. Without that information, the posted label and partial interval do not allow readers to independently assess the non-inferiority criterion.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when data vary more than a statistical model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow; if it accounts for excess variability, uncertainty can be more realistic. This primary outcome is continuous, and the record reports standard deviations rather than a count model. No over-dispersion assessment or adjustment is reported, so it should not be assumed to have been performed or to be necessary for this analysis.

What does randomization contribute?

Random allocation is intended to make the comparison groups similar on average at the start of a study, including characteristics that may not be measured. The registry identifies the study as randomized, but the random sequence generation, allocation concealment, and any stratification factors are not reported. Randomization strengthens the design of a comparative trial, but it does not ensure that every group characteristic will be identical, nor does it resolve questions about missing outcomes or analysis choices.

What is the role of masking?

The study is labelled double-masked. Masking can reduce the influence of expectations on assessments or study conduct, depending on who is masked and how. The registry record does not state which parties were masked or provide details of the masking process. Because the endpoint is based on a visual acuity test, the exact assessment procedures are relevant, but the posted record does not provide information beyond the described chart, refraction, distance, and lighting conditions.

The reported endpoint is subject-based and combines both eyes into one score. That avoids treating two eyes from one participant as independent observations in the primary endpoint, but the registry does not give further information about the calculation of the binocular score. The outcome population is described as participants with data at the visit. The analysis method, missing-data assumptions, and any sensitivity analyses are not reported in the registry record.

Finally, the registry gives one primary outcome and one posted analysis, and lists no secondary outcomes posted. That does not establish whether additional analyses were conducted or whether interim analyses occurred. Such details, along with a prespecified statistical analysis plan, are not reported in the registry record.

10. Confidence Intervals and Precision

The recalculated mean difference is 0.045 logMAR for the contrast Eyhance minus Clareon. Its confidence interval excludes zero, and the unadjusted p-value is <0.001. The interval describes uncertainty around the estimated average difference under the assumptions of the unadjusted calculation. It is more informative than the point estimate alone because it indicates that the estimate is not exact and that a range of values is compatible with the observed data.

The interval’s endpoints are reported in the registry-derived calculation with more than three decimal places, so they are not repeated. The registry’s sponsor-reported non-inferiority analysis gives an estimate of -0.045 and a 95% confidence interval upper limit of -0.024, but the other limit is not reported in the registry record. A one-sided limit alone does not show the complete interval or allow an independent assessment of the full precision of that estimate.

Precision is affected by the spread of the outcome and by the number of observations contributing to the analysis. The outcome counts are 86 for the Clareon group and 81 for the Eyhance group. The registry does not report a detailed account of participants without month 3 data or the method used to handle missing values. The confidence interval from the unadjusted recalculation therefore should be read as conditional on the posted group summaries and its calculation assumptions.

Statistical precision and clinical importance are different. A confidence interval that excludes zero does not show whether a difference is large enough to matter in practice. The registry record does not report a clinically meaningful threshold for logMAR BCDVA, so the posted statistical evidence cannot establish that interpretation on its own.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For this continuous-outcome comparison, the entries are participants per arm, not total events. The registry record does not report the original sample-size justification or the trial’s own design assumptions.

The illustrations 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 row for 100% of the observed effect uses participants per arm of 51 for 80% power and 68 for 90% power. The row for 75% of the observed effect uses 90 participants per arm for 80% power and 120 for 90% power. The row for 50% of the observed effect uses 201 participants per arm for 80% power and 269 for 90% power.

In plain language, the 80% power column illustrates the per-arm size that would give an 80% chance of detecting the chosen effect under the stated assumptions if that effect were present. The 90% power column gives the corresponding illustration for a 90% chance. These are prospective planning concepts, not descriptions of what happened in this trial. The illustrations are not observed power.

The pattern conveys an important general principle: smaller effects are harder to distinguish from random variation, so detecting them with the same power generally requires more participants. These illustrations use the observed effect as their starting point and should not be read as proof that the trial was designed around that effect or that the original design had these 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 = 0.045; pooled standard deviation σ = 0.080.
2. n = 2 × (1.96 + 0.842)² × 0.080² / 0.045² = 50.2, rounded up to 51 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 <- 0.045                      # observed difference in means
sigma <- 0.0804670005767469                     # 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(5481125)
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 = 51 (80% power), 68 (90% power)
 75% of observed effect: n per arm = 90 (80% power), 120 (90% power)
 50% of observed effect: n per arm = 201 (80% power), 269 (90% power)
power.t.test: 51.2 
Simulated power at n = 51 per arm: 0.798 (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 registry posts a sponsor analysis labelled non-inferiority, with a mean difference for final values of -0.045 and a reported 95% confidence interval upper limit of -0.024. It does not report the other confidence limit, a p-value, the analysis method, or the non-inferiority margin. The registry record also does not state the contrast direction for this analysis.

The simple recalculation from the posted group means expresses the difference as Eyhance minus Clareon and gives 0.045 logMAR. The sign is opposite to the sponsor’s posted estimate, while the absolute estimate is 0.045 in both displays. This is consistent with a difference in group ordering, but the registry does not explicitly confirm that explanation. The recalculation is unadjusted and should not be treated as a reconstruction of the sponsor’s analysis.

Because the sponsor’s own analysis is reported, it takes precedence over a simple unadjusted recalculation when describing the sponsor’s findings. However, the partial interval and unreported method limit independent assessment of the analysis. The registry does not report the prespecified margin or analysis details needed to assess how the non-inferiority conclusion was determined.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and one posted analysis, and indicates that no secondary outcomes are posted. This limited record does not establish that no additional outcomes or analyses were considered during the study. The number of interim analyses, any stopping rules, and the complete prespecified statistical analysis plan are not reported in the registry record.

Multiplicity arises when several outcomes, comparisons, or analyses are tested. General statistical explanation: testing multiple hypotheses can increase the chance of at least one apparently unusual result by chance, so a study may prespecify a strategy for controlling that risk. No multiplicity adjustment or strategy is reported in the registry record. With only the posted primary result, it is not possible to determine whether the analysis belongs to a broader family of tests or whether any adjustment was planned.

The outcome population is described as “AAS with data at visit.” The meaning of AAS is not reported in the registry record. The listed outcome counts are 86 for Clareon/Clareon Toric and 81 for Eyhance/Eyhance Toric, while total enrollment is 203. The registry does not explain these differences, give reasons for missing visit data, or state whether the analysis followed an intention-to-treat, per-protocol, or other population definition.

The missing-data method and assumptions are not reported in the registry record. The record does not say whether missing values were imputed, whether participants with incomplete data were excluded, or whether sensitivity analyses assessed the effect of missingness. These details matter because a complete-visit analysis can describe participants with recorded results without necessarily representing all randomized participants.

The registry also does not report baseline characteristics, subgroup analyses, covariate adjustment, or any sensitivity analyses for the primary endpoint. Their absence from the posted record should not be interpreted as evidence that they were or were not part of the full study 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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ciliary zonular weakness (1.2%), cystoid macular oedema (1.2%), fall (1.2%), hip fracture (1.2%), intraocular pressure increased (1.2%).

The registry reports serious adverse events by period and group. In the Clareon/Clareon Toric first-eye group, 2 serious events were reported among 89 at risk; the second-eye group reports 0 among 86, and the systemic group reports 2 among 89. In the Eyhance/Eyhance Toric first-eye group, 2 serious events were reported among 86 at risk; the second-eye group reports 0 among 84, and the systemic group reports 3 among 86. The pretreatment group reports 0 serious events among 175 at risk.

These are the registry’s period-specific counts, not a direct estimate of comparative risk between the lens groups. The groups refer to first-eye, second-eye, systemic, and pretreatment reporting periods, so they should not be combined into a single between-group comparison. The registry also lists no deaths in the reported groups.

The serious-event terms listed with percentages of 1.2% include Ciliary zonular weakness, Cystoid macular oedema, Fall, Hip fracture, Intraocular pressure increased, and Hypomagnesaemia. These entries describe reported events and do not establish that an event was caused by a study lens or procedure. The record does not provide a comparative statistical analysis of adverse events, event timing details, or a fuller account of causality assessment.

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

The posted data show that the mean month 3 binocular BCDVA was -0.1 logMAR in the Clareon/Clareon Toric group and -0.055 logMAR in the Eyhance/Eyhance Toric group. Since lower values indicate better measured acuity, the mean value was lower in the Clareon group. The unadjusted recalculated difference, expressed as Eyhance minus Clareon, is 0.045 logMAR, with an unadjusted p-value of <0.001 and a confidence interval that excludes zero.

Those results describe a statistical contrast in average visual acuity among participants with a posted visit result. They do not describe the experience of every participant, and the registry does not report a threshold for a clinically important difference. Statistical evidence against a zero difference cannot, by itself, establish whether the magnitude matters clinically.

The registry also posts a sponsor non-inferiority analysis, but the method, margin, and one confidence limit are not reported in the registry record. The sponsor’s own analysis takes precedence over the unadjusted recalculation when considering that analysis, but the available information does not allow a full independent assessment of its non-inferiority framework.

The results should be read in the context of the outcome population and missing-data information. Total enrollment is 203, while outcome results are posted for 86 and 81 participants in the two groups. The registry does not explain the difference or describe missing-data handling. The posted outcome therefore should not be assumed to represent a specified analysis of all randomized participants.

The safety listings report serious-event counts across different periods and groups. They are descriptive and do not provide a direct comparative safety estimate. Neither the efficacy summaries nor the safety counts alone resolve the limitations created by unreported analysis details, missing-data methods, or clinical importance thresholds.

17. Why This Trial Matters Statistically

This trial illustrates how a continuous endpoint can be summarized in a way that is statistically precise but still requires careful interpretation. The group means and mean difference provide an understandable account of the average month 3 outcome, while the confidence interval and p-value describe uncertainty under the recalculation’s assumptions. The direction of the logMAR scale is essential: lower values represent better measured acuity, so a positive contrast expressed as Eyhance minus Clareon means the Eyhance group had a higher average logMAR value.

It also shows why the group order and sign of a difference must be made explicit. The sponsor’s posted estimate is -0.045, while the simple unadjusted recalculation is 0.045 when expressed as Eyhance minus Clareon. The difference in sign may reflect contrast ordering, but the registry does not state the sponsor contrast direction. A number without a defined comparison order can be easy to misread.

The registry’s non-inferiority label raises a separate methodological issue. Non-inferiority depends on a prespecified margin and an analysis method, neither of which is reported in the registry record. The sponsor’s estimate and partial confidence interval therefore cannot be fully evaluated from the posted details alone. This is an example of why a point estimate alone is not enough to interpret a non-inferiority claim.

Finally, the distinction between total enrollment and the outcome population is important. The primary endpoint is reported among participants with visit data, but the handling of missing results is not described. Readers need both the numerical result and enough information about the analysis population, missingness, and prespecified methods to understand the scope of the evidence.

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.

Several trial-specific details that would help interpret the primary result are not reported in the registry record. These include the randomization procedure, allocation concealment, which parties were masked, the original sample-size justification, and the complete statistical analysis plan. The record identifies the study as randomized and double-masked but does not describe these implementation details.

The total enrollment is 203, whereas the primary outcome is reported for 86 participants in the Clareon group and 81 in the Eyhance group. The reason for the difference, the number of participants without month 3 data, and the handling of missing observations are not reported in the registry record. The stated population description includes an acronym that is not defined in the record.

The sponsor’s analysis is labelled non-inferiority, but its method, margin, complete confidence interval, and p-value are not reported in the registry record. This prevents independent evaluation of the non-inferiority criterion. The registry’s contrast direction is also not specified, making the sign difference from the unadjusted recalculation harder to interpret definitively.

No clinically important difference threshold is reported for BCDVA. The registry also does not report baseline results, covariate adjustment details, sensitivity analyses, subgroup results, interim analyses, or multiplicity procedures. Their absence from the record does not establish whether they were performed in the full study.

Safety data are listed by different periods and groups rather than as a direct comparative analysis. The registry does not provide a comparative estimate, fuller event-level context, or details of causality assessment. The posted counts should therefore be read as descriptive reporting rather than as a complete comparison of safety between lens families.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clareon Toric vs Eyhance Toric — NCT05481125.
• Registry record last updated 2024-10-30; status last verified 2024-10.
• Results first posted 2024-10-30.
• 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

NCT05481125 is a completed, randomized, double-masked, parallel-group study sponsored by Alcon Research. It enrolled 203 participants and compared Clareon/Clareon Toric intraocular lenses with Eyhance/Eyhance Toric intraocular lenses following phacoemulsification surgery.

The primary outcome was mean binocular BCDVA at 4 meters under bright lighting at the month 3 postoperative visit, measured in logMAR. The posted means were -0.1 in the Clareon group and -0.055 in the Eyhance group, with outcome counts of 86 and 81, respectively. The unadjusted recalculated difference for Eyhance minus Clareon is 0.045 logMAR, with p < 0.001.

The registry also reports a non-inferiority analysis, but does not report its method, margin, or complete confidence interval. Details of the original sample-size rationale and missing-data handling are not reported in the registry record.