Clareon PanOptix Pro vs. Clareon PanOptix - Study A: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clareon PanOptix Pro vs. Clareon PanOptix - Study A (NCT06400745), a randomized na study. The primary outcome is Mean Monocular Photopic Best Corrected Distance Visual Acuity (BCDVA).

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel-design device study listed as phase NA. Alcon Research was the sponsor. The registry record lists the study as completed, with a start date of 2024-06-18 and primary completion date of 2024-12-13. It reports enrollment of 87 participants and two lens interventions, alongside cataract surgery as a procedure.

The contralateral arrangement is central to understanding the comparison. Each participant was assigned a first-eye lens at random and was to receive the other lens in the fellow eye. In one sequence, CPO Pro IOL was implanted first and CPO IOL in the fellow eye; in the other sequence, the order was reversed. The second surgery was planned approximately 7-14 days after the first. This design allows outcomes from the two lens types to be measured within the same participant, while the randomized sequence helps distribute order across participants.

The primary outcome analysis reports 83 eyes in each lens group. The registry labels the analysis population the All-Implanted Analysis Set. It does not explain the difference between enrollment and the numbers analyzed, or specify the number of participants contributing a complete paired set of measurements. The outcome was measured at Month 2 postoperative. Masking is described as double, but the identities of the masked parties and the operational masking procedures are not reported in the registry record.

The listed primary endpoint is a continuous measure: mean monocular photopic BCDVA in logMAR. One outcome measure and one analysis are posted. The registry record does not report the original sample-size justification, the details of the randomization procedure, or whether any interim analyses were planned or conducted. Those omissions limit conclusions about how the trial was planned and how its reported analysis relates to its original 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 87 randomized participants, 4 were discontinued after randomization and prior to attempted implantation. This reporting group includes all participants with attempted implantation (83).

Overall Study

Analysis population for the primary outcome, as defined in the registry: All-Implanted Analysis Set

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

6. Primary Endpoint

The registry lists the primary outcome as Mean Monocular Photopic Best Corrected Distance Visual Acuity (BCDVA), measured over Month 2 postoperative.

Monocular photopic BCDVA measures distance visual acuity for an individual eye with correction in place, under well-lit conditions. In this study, acuity was assessed using Early Treatment Diabetic Retinopathy Study (ETDRS) reading charts at a distance of 4 meters. The result was recorded in logarithm Minimum Angle of Resolution (logMAR). The registry describes logMAR values as typically ranging from -0.3, corresponding to 20/10 vision on the Snellen chart, to 1, corresponding to 20/200 vision; lower scores indicate better vision.

BCDVA is used to quantify how clearly an eye can see at distance when refractive correction is in place. Reporting a group mean describes the average measured acuity, while the standard deviation describes variation among the observations. This endpoint is monocular: it concerns each eye separately, rather than a combined binocular visual outcome. The measurement conditions and correction status matter because acuity can differ depending on lighting and whether correction is used.

The primary time point was Month 2 postoperative. The registry record gives the time point but does not report whether additional timing windows, repeated-measure procedures, or rules for measurements outside the target visit were specified. A mean comparison at one postoperative time point also does not, by itself, describe the full course of visual acuity over time or other dimensions of vision.

7. Results Posted in the Registry

• CPO IOL: mean 0.02 versus 0.03 on control; difference -0.01 (95% CI -0.04 to 0.02), standardized effect d = -0.10; z-test p = 0.504.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary measure is continuous, so it is described using a mean and standard deviation. A mean provides a measure of the central level of a continuous outcome; a standard deviation describes how spread out individual measurements are around that mean. In this study, the outcome is logMAR BCDVA, and lower values indicate better acuity. The posted means are 0.032 for CPO Pro IOL and 0.023 for CPO IOL. The registry gives standard deviations of 0.092 and 0.081, respectively; these are reported in the record but are not needed to interpret the direction of the means.

What does a difference in means represent?

A difference in means subtracts one group’s average from the other’s. The recalculated comparison uses CPO IOL minus CPO Pro IOL, yielding -0.009 logMAR. A negative result therefore means the posted mean for CPO IOL is lower under that orientation. Reversing the subtraction reverses the sign, not the underlying comparison. This is why the sponsor’s positive difference of 0.009 is not a contradictory direction: its comparison is oriented CPO Pro IOL relative to CPO IOL.

In general, a difference in means is an estimate of the average contrast between the compared groups. It is not a measure of the spread of individual outcomes, and it does not imply that every participant’s two eyes differ by that amount. In a contralateral design, both lens outcomes come from eyes of the same participant. A paired analysis can use the within-participant relationship between eye measurements. The registry’s posted summary statistics do not include the within-participant covariance needed to reconstruct that paired uncertainty calculation.

What does the confidence interval convey?

In general, a confidence interval represents uncertainty in an estimate under a specified statistical method and its assumptions. A narrower interval indicates greater precision for the estimated quantity; a wider interval indicates more uncertainty. The recalculated interval includes zero, so it is compatible with no mean difference as well as with differences in either direction. It should not be interpreted as a prediction interval for individual eyes or as proof that all values inside it are equally plausible in every sense.

The sponsor’s posted analysis is a one-sided t-test for non-inferiority. In general, non-inferiority testing evaluates whether an outcome for one treatment is not worse than a comparator by more than a prespecified margin. The margin defines the largest difference that would still satisfy the chosen criterion. A confidence bound is compared with that margin according to the test’s direction and specification. The registry record does not report the margin, so the posted upper bound cannot by itself establish the sponsor’s decision.

Why distinguish the recalculation from the sponsor analysis?

The recalculated mean difference is an unadjusted analysis based on the posted group summary statistics. It gives a conventional two-sided comparison with a p-value of 0.504 and a confidence interval. The sponsor’s analysis is reported as a one-sided non-inferiority test, with a different orientation and incomplete inferential details. The two approaches address different hypotheses and need not present estimates in the same direction. A p-value from a two-sided test is not a substitute for a non-inferiority margin or a one-sided decision rule.

Because the study is contralateral, a simple comparison treating eye groups as unrelated may not represent the design’s full paired structure. In general, accounting for pairing can improve or reduce precision depending on how strongly measurements from two eyes in one participant are related. That relationship is not reported in the registry record. The recalculated uncertainty therefore should be understood as a summary-statistic recalculation, not as a recovery of an undocumented paired model.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than the statistical model expects. If a model assumes less variability than the data actually contain, it can understate uncertainty and make estimates appear more precise than warranted. For a continuous outcome, the standard deviation is one way to describe observed spread; other models may also need to account for clustering or repeated measurements. This study’s outcome is measured in two eyes per participant, so within-person dependence is a design consideration. The registry record does not report an over-dispersion assessment or a model adjustment for within-participant dependence. The concept is relevant as a general statistical caution, not as a claim that over-dispersion was found in this study.

The all-implanted analysis population is named, but its detailed inclusion rules are not reported. In general, an analysis population specifies which randomized or treated participants contribute to an estimate. Different analysis sets can answer different questions, and exclusions after randomization may affect comparability. The registry record does not describe exclusions, missing measurements, or sensitivity analyses, so the impact of those issues cannot be assessed from the posted outcome details.

10. Confidence Intervals and Precision

The recalculated difference in mean BCDVA was -0.009 logMAR for CPO IOL relative to CPO Pro IOL. Its 95% confidence interval extends across zero, and the unadjusted p-value was 0.504. The interval therefore does not isolate a single direction of difference. It reflects uncertainty in the estimated group-level contrast, not uncertainty about the recorded means themselves.

The registry’s exact recalculated interval endpoints are more precise than three decimal places and are not repeated. In plain terms, its lower endpoint is negative and its upper endpoint is positive. This means the interval includes no difference as well as values favoring either lens according to the lower-is-better scale. The registry record does not provide a threshold for a clinically meaningful BCDVA difference, so the interval cannot be classified as excluding or including such a threshold.

Precision is distinct from statistical significance and clinical importance. A confidence interval is generally a way to express how much uncertainty surrounds an estimate under the method’s assumptions. An interval that includes zero does not prove that the true effect is zero; it means the posted analysis does not rule out zero at its stated confidence level. Likewise, a point estimate close to zero does not establish equivalence. Equivalence requires a prespecified acceptable range and a design and analysis that test that question.

The study used a contralateral design, but the recalculated interval comes from posted summary statistics rather than a reported within-participant analysis. The correlation between the two eyes’ measurements is not reported in the registry record. As a result, the interval should not be treated as a reconstruction of a paired confidence interval. The sponsor’s non-inferiority analysis gives a one-sided upper bound of 0.023, but its margin and full decision criteria are not reported, so the precision information does not independently settle a non-inferiority conclusion.

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, the figures are participants per arm, not total events. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. It uses the stated fraction of the observed effect as the effect to detect. The original sample-size justification and assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the assumed effect, if that effect and the calculation assumptions held. The 90% power column gives the corresponding planning count for a 90% chance. These are design probabilities under assumptions, not guarantees about the result of a future study. The rows show planning for 100%, 75%, and 50% of the observed effect. As the assumed effect becomes smaller, more participants are needed to distinguish it from random variation at the same significance level and target power.

The calculation uses the effect estimated in this study as its starting point. That estimate is uncertain, and planning around an observed effect can produce an unstable illustration, especially when the observed effect is small. The displayed figures should therefore be read as conditional scenarios, not as a definitive recommendation for a future trial. They do not account for design features that are not included in the stated assumptions, such as the within-participant correlation in this contralateral study. They are not observed power.

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 = -0.009; pooled standard deviation σ = 0.087.
2. n = 2 × (1.96 + 0.842)² × 0.087² / -0.009² = 1,458.9, rounded up to 1,459 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 <- -0.009                      # observed difference in means
sigma <- 0.0867620308660419                     # 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(6400745)
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 = 1,459 (80% power), 1,953 (90% power)
 75% of observed effect: n per arm = 2,594 (80% power), 3,472 (90% power)
 50% of observed effect: n per arm = 5,836 (80% power), 7,812 (90% power)
power.t.test: 1459.8 
Simulated power at n = 1,459 per arm: 0.806 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor’s own analysis is reported as a one-sided t-test for non-inferiority. It gives a difference in means of 0.009, with a 95.1% confidence interval whose upper bound is 0.023. The registry record does not report the lower bound or a p-value for that analysis. Its difference is oriented as CPO Pro IOL relative to CPO IOL, whereas the recalculated comparison is CPO IOL relative to CPO Pro IOL and is -0.009. The sign difference reflects the direction of subtraction.

The recalculation gives an unadjusted two-sided p-value of 0.504 and an interval spanning zero. That is not the same test as non-inferiority. A non-inferiority conclusion depends on a prespecified margin, which is not reported in the registry record. The upper confidence bound cannot be judged against an unreported threshold, and the registry’s posted information does not allow an independent determination of whether the sponsor’s criterion was met.

The recalculation is a simple unadjusted analysis of the posted summary statistics; it does not replace the sponsor’s analysis. The discrepancy flag is false, but differences in test objective and estimate orientation still matter when comparing the results. The sponsor’s analysis is the trial’s reported analysis; the recalculation offers a separate statistical description rather than a correction to it.

14. Multiplicity, Missing Data and Analysis Populations

The registry record posts one primary outcome measure and one analysis, with no secondary outcomes posted. The primary outcome is mean monocular photopic BCDVA at Month 2 postoperative. With only one posted outcome analysis, the registry information does not present a set of multiple outcome tests whose adjustment can be evaluated. However, the record does not state whether the protocol included other planned outcomes or comparisons, nor whether a multiplicity strategy was specified.

Multiplicity arises in general when several hypotheses are tested, because the chance of at least one apparently notable result can increase as more tests are considered. Study plans may address this through a prespecified testing order or statistical adjustment. Whether such procedures were planned or used is not reported in the registry record. The number of posted outcomes alone cannot establish the complete scope of planned analyses.

The primary outcome population is named as the All-Implanted Analysis Set. The detailed definition of that set, including how participants or eyes were included or excluded, is not reported. The registry lists 87 enrolled participants and 83 observations in each lens group for the primary outcome. It does not explain the difference between those figures or state how many participants had measurements available for both eyes.

Missing-data counts, reasons for missingness, imputation procedures, and sensitivity analyses are not reported in the registry record. In general, missing outcomes can affect a comparison if the availability of measurements is related to the outcome or differs across groups. The available record does not show whether that concern arose in this study, so no assumption about the missing measurements is warranted.

The record also does not report the original statistical analysis plan, interim analyses, or any adjustment for the within-participant structure of the contralateral design. These omissions do not establish that such procedures were absent; they mean the registry record does not describe them. Consequently, the posted results can be read as the reported outcome analysis, but details needed to assess all planned tests, missing-data handling, and population definitions are unavailable.

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: cystoid macular oedema (1.2%), dry age-related macular degeneration (1.2%), epiretinal membrane (1.2%), halo vision (1.2%), vitreoretinal traction syndrome (1.2%).

The registry reports serious adverse events by category, with 83 participants at risk in each listed group. Pretreatment has 0 serious adverse events and 0 other adverse events. For the CPO Pro IOL Model PXYWT0 group, 1 participant was affected by a serious adverse event and 6 by other adverse events. For CPO IOL Model CNWTT0, the corresponding counts are 3 and 8. The systemic group reports 2 participants affected by serious adverse events and 0 by other adverse events. No deaths are reported in any of the listed groups.

The registry lists six serious adverse event terms at 1.2% each: cystoid macular oedema, dry age-related macular degeneration, epiretinal membrane, halo vision, vitreoretinal traction syndrome, and intestinal obstruction. These are event-term entries, not a basis for adding counts across categories. The record does not clarify whether a participant could contribute to more than one term or category, so the figures should be read within their reported groupings rather than combined into a new total.

These counts describe the posted safety record, not a comparative estimate adjusted for exposure or other factors. The registry does not provide additional information about event timing, severity beyond the serious classification, relatedness, duration, or resolution. The counts alone cannot establish a causal relationship to a lens or procedure, nor can they settle broader safety questions.

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

The posted outcome means show average Month 2 postoperative monocular photopic BCDVA of 0.032 logMAR for CPO Pro IOL and 0.023 for CPO IOL. Because lower logMAR values indicate better acuity, the numerical direction favors the lower mean for CPO IOL. The recalculated difference is -0.009 for CPO IOL relative to CPO Pro IOL. The uncertainty interval spans zero, and the unadjusted two-sided p-value is 0.504.

These results do not establish that the lenses are identical or equivalent. A nonsignificant difference test does not demonstrate absence of a meaningful difference. Equivalence would require a defined acceptable range and an analysis designed to test whether the difference lies within it. Similarly, a non-inferiority claim requires a prespecified margin and a decision rule. Although the registry reports a sponsor non-inferiority analysis, the margin is not reported, so its criterion cannot be assessed from the record.

The results also do not show that every participant or eye had the group mean acuity. A mean is an average, while individual measurements vary. The endpoint concerns monocular, corrected visual acuity under photopic conditions at a particular postoperative time point; it does not represent binocular vision, uncorrected acuity, all visual functions, or outcomes at other time points.

The primary outcome analysis includes 83 eyes in each lens group, and the registry reports 87 enrolled participants. The record does not explain the analysis population in enough detail to determine how the enrollment and outcome counts relate or how missing measurements were handled. It also does not provide the within-participant correlation needed to reconstruct a paired analysis from the posted summaries.

Accordingly, the statistical result describes a small numerical mean contrast with uncertainty that includes zero under the recalculated comparison. It cannot, by itself, establish clinical importance, equivalence, non-inferiority, individual benefit, or a causal explanation for any adverse event. Those conclusions require criteria and details that are not reported in the registry record.

17. Why This Trial Matters Statistically

This study is statistically notable for its contralateral design: each participant was intended to receive both lens types, one in each eye, with the order randomized. Such a design can make within-participant comparisons informative because characteristics shared by a participant are held constant across the two eyes. At the same time, analysis should account for the fact that two eye measurements from one person may be related. The registry record does not report the within-participant correlation or enough analysis detail to determine how that dependence was handled.

The primary outcome is continuous and has a directional scale: lower logMAR indicates better acuity. Correctly interpreting the sign of a mean difference therefore depends on knowing which lens is subtracted from which. The recalculated estimate is CPO IOL minus CPO Pro IOL, while the sponsor’s reported estimate uses the reverse orientation. Both can describe the same numerical contrast with opposite signs.

The record also illustrates why a conventional difference test and a non-inferiority test should not be conflated. The recalculated two-sided test asks whether the mean difference is distinguishable from zero. The sponsor analysis is described as a one-sided non-inferiority test, which requires a margin. Because the margin is not reported, the posted result cannot be fully evaluated as a non-inferiority decision from the registry information alone.

Finally, the sample-size illustrations make explicit that planning depends on the effect size a future study aims to detect. Smaller target effects require more participants under the stated assumptions. These calculations are not the original trial justification and are not observed power. Together, the design and statistical reporting emphasize the importance of specifying the analysis population, dependence structure, decision thresholds, and planning assumptions when interpreting a clinical comparison.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The main limitation for interpretation is incomplete reporting of the sponsor’s non-inferiority framework. The registry identifies a one-sided t-test and gives an upper confidence bound, but does not report the non-inferiority margin or the full decision rule. Without that threshold, the analysis cannot be classified as meeting or not meeting its intended criterion from the registry record.

The trial is contralateral, but the posted outcome summaries do not report the within-participant correlation or the method used to account for paired eyes. The recalculated comparison is based on summary statistics and should not be mistaken for a paired reanalysis. This matters because eye measurements within a participant may be related, and that relationship can affect uncertainty.

The registry reports 87 participants enrolled and 83 observations in each lens group for the primary outcome, but does not explain the analysis-set flow, whether all analyzed observations form complete pairs, or how missing data were handled. It also does not provide baseline outcome information, detailed eligibility criteria, or the full analysis population definition. These gaps restrict assessment of exclusions and representativeness.

Only one outcome measure and one analysis are posted, and no secondary outcomes are posted. The record does not provide the protocol-level list of planned outcomes, a multiplicity strategy, an interim-analysis plan, or the original sample-size justification. Their absence from the registry information should not be interpreted as proof that none existed.

The endpoint is limited to corrected monocular photopic distance acuity at Month 2 postoperative. It does not by itself characterize other visual conditions, binocular outcomes, or longer-term results. The safety information is also presented as counts by event group, without further details on timing, relatedness, or overlap among event terms. These are limitations of what the registry record reports, not evidence that unreported procedures or outcomes were absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clareon PanOptix Pro vs. Clareon PanOptix - Study A — NCT06400745.
• Registry record last updated 2025-12-12; status last verified 2025-12.
• Results first posted 2025-12-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT06400745, titled “Clareon PanOptix Pro vs. Clareon PanOptix - Study A,” is a completed randomized, double-masked, parallel-design device study sponsored by Alcon Research. The study enrolled 87 participants and compared two trifocal intraocular lenses in a contralateral arrangement, with randomized first-eye lens assignment and the other lens implanted in the fellow eye approximately 7-14 days later.

The primary outcome was mean monocular photopic BCDVA in logMAR at Month 2 postoperative, in the All-Implanted Analysis Set. The posted means were 0.032 for CPO Pro IOL and 0.023 for CPO IOL, with 83 observations in each group. The recalculated difference was -0.009 for CPO IOL relative to CPO Pro IOL; its interval spans zero and its unadjusted p-value was 0.504.

A sponsor one-sided non-inferiority analysis is also posted, but its margin is not reported. The registry record does not report the original sample-size justification, missing-data procedures, or the within-participant correlation needed to reconstruct a paired analysis.