Evaluate the Safety and Effectiveness of the enVista® One-Piece Hydrophobic Acrylic Trifocal Intraocular Lens: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluate the Safety and Effectiveness of the enVista® One-Piece Hydrophobic Acrylic Trifocal Intraocular Lens (NCT03603600), a randomized na study. The primary outcome is Photopic Monocular Best-corrected Distance Visual Acuity (BCDVA).

2. Clinical Question

3. Trial Design

This was a prospective, multicenter, randomized, active-controlled, double-masked, parallel-group study. Its listed phase is NA. The registry title and design fields describe random assignment to one of two intraocular lens devices, with subjects followed in parallel groups. The study status is completed, and the record gives an enrollment of 501.

The two devices were enVista MX60EF, described as a trifocal multifocal lens, and enVista MX60E, described as a monofocal lens. The registry reports the primary endpoint means for 312 subjects in the trifocal group and 156 in the monofocal group. These endpoint-specific counts are not the same as the total enrollment. The record does not explain the difference in numbers, so it would be inappropriate to attribute it to a particular reason, such as withdrawal, missing measurements, or a defined analysis population.

The registry lists the study start as 2018-05-31 and primary completion as 2023-05-04. Those dates describe the study record, but do not by themselves establish how long each participant was followed. The primary outcome timeframe is specified relative to the second-eye and first-eye implantations, and individual follow-up schedules are not reported in the registry record.

Randomization can help make treatment groups comparable on average, while masking can reduce some forms of measurement or care-related bias. Those are general design principles; the registry does not state the randomization method, allocation concealment procedures, or exactly who was masked. It also does not give site-level enrollment or explain whether the analysis accounted for differences among centers. The stated design therefore supports describing the study as randomized and double-masked, but not reconstructing details that the record does not report.

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.

Overall Study

Reasons for not completing this period:

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.

6. Primary Endpoint

The registry lists the primary outcome as Photopic Monocular Best-corrected Distance Visual Acuity (BCDVA), measured over Day 120 to Day 180 after second eye implantation, up to 210 days from first eye implantation at Baseline..

The primary endpoint is photopic monocular best-corrected distance visual acuity, abbreviated BCDVA, reported as a mean in logMAR. It was assessed in first eyes at Post-Operative Visit 4, within the stated window of Day 120 to Day 180 after second-eye implantation, up to 210 days from first-eye implantation at baseline. Photopic indicates measurement under light conditions, monocular indicates assessment of an individual eye, and best-corrected means visual acuity is measured with correction. These are general descriptions of the endpoint terminology.

Distance visual acuity is used to characterize the clarity of distance vision. Best-corrected measurement focuses on acuity under correction rather than uncorrected vision; the endpoint thus describes visual acuity in a defined measurement condition. In general, logMAR is a scale used to express visual acuity, and lower values correspond to better acuity. That scale interpretation helps read the direction of the posted means, but does not alone establish how important a difference is to patients.

The registry does not report a threshold for a clinically meaningful change, a margin for noninferiority, or a rationale explaining why this endpoint was selected as primary. The endpoint is one measure of visual performance and does not summarize every aspect of vision, safety, or patient experience. It should be read alongside the secondary outcomes and the safety information, while recognizing that those other measures answer different questions.

7. Results Posted in the Registry

• enVista MX60E: mean -0.02 versus 0.02 on control; difference -0.04 (95% CI -0.06 to -0.02), standardized effect d = -0.42; 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.

Photopic Binocular DCNVA at 40 cm at Postoperative Visit 4

• 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:
  • enVista MX60E: mean 0.45 versus 0.08 on control; difference 0.37 (95% CI 0.35 to 0.40), standardized effect d = 3.14; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for enVista MX60E than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Photopic Binocular UNVA at 40 cm at Postoperative Visit 4

• 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:
  • enVista MX60E: mean 0.42 versus 0.10 on control; difference 0.32 (95% CI 0.30 to 0.35), standardized effect d = 2.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for enVista MX60E than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Photopic Binocular DCIVA at 66 cm at Postoperative Visit 4

• 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:
  • enVista MX60E: mean 0.27 versus 0.04 on control; difference 0.23 (95% CI 0.20 to 0.25), standardized effect d = 1.94; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for enVista MX60E than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question beyond monocular best-corrected distance acuity. The registry lists binocular near and intermediate visual-acuity measures at Postoperative Visit 4, as well as first-eye measures at a later postoperative visit. These endpoints address different viewing distances, testing conditions, and units of observation. They can provide complementary descriptions of visual performance, but they should not be treated as interchangeable versions of the primary endpoint.

Across the three secondary result summaries, the displayed mean differences are in the direction of lower logMAR means for the trifocal group than for the monofocal group, and each has an unadjusted p-value of <0.001. This broad pattern is directionally different from the primary distance BCDVA comparison. The secondary outcomes thus add context rather than simply repeating the primary finding: different visual tasks can yield different relative group patterns. Their meaning remains tied to their own endpoint definitions and postoperative assessment windows.

These secondary comparisons carry less inferential weight than a primary result when many outcomes are examined without a reported adjustment for multiplicity. Testing several outcomes increases the chance that at least one result appears statistically notable by chance. The registry does not report a multiplicity procedure or a hierarchy specifying which secondary questions were confirmatory. The displayed unadjusted p-values should therefore be read as descriptive evidence for each comparison, not as family-wise controlled evidence across all secondary outcomes.

The registry names additional secondary measures, but the numeric summaries do not cover every listed outcome. The record does not report a complete set of results for every listed secondary measure in the outcome details used for this page. Results for those measures should not be assumed from the outcomes that are shown. A coherent pattern across related outcomes can be informative, but it does not eliminate concerns about multiplicity, selective reporting, or the absence of a stated analysis plan.

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

• Photopic Binocular DCNVA at 40 cm at Postoperative Visit 4
• Photopic Binocular UNVA at 40 cm at Postoperative Visit 4
• Photopic Binocular DCIVA at 66 cm at Postoperative Visit 4
• Photopic Binocular UIVA at 66 cm at Postoperative Visit 4
• First-eye BCDVA Evaluated at Postoperative Visit 5
• First-eye DCNVA Evaluated at Postoperative Visit 5
• First-eye DCIVA Evaluated at Postoperative Visit 5

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a continuous measurement summarized by its mean and standard deviation in each group. For a continuous outcome, the group mean describes the central average, while the standard deviation describes how spread out individual observations are around that average. These quantities answer different questions: the mean describes the location of the group results, and the standard deviation describes their variability. Neither alone describes the full distribution of individual outcomes.

What does the mean difference represent?

The reported comparison is a mean difference. Here, the stated arm ordering corresponds to the monofocal group mean minus the trifocal group mean. A difference of zero would represent identical group means; a value below zero indicates that the mean in the monofocal group is numerically lower than the mean in the trifocal group. For logMAR, lower values generally correspond to better visual acuity, but interpreting a numerical direction is not the same as deciding whether a difference is meaningful to patients. The registry does not state a clinical-importance threshold.

A mean difference condenses the comparison to one number and is expressed in the outcome's original units, logMAR. It is directly interpretable alongside the group means, but it does not reveal whether the distributions overlap, whether there are subgroups with different results, or how individual participants' outcomes varied. The posted standard deviations help convey spread, although a complete assessment of distributions would require more information than the registry summary supplies.

How should the confidence interval be read?

A confidence interval expresses uncertainty around an estimated effect under a statistical procedure and its assumptions. In general, a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the effect's size. The interval reported for the primary mean difference runs from -0.057 to -0.021. Its placement entirely on one side of zero indicates that the displayed interval does not include no mean difference. It does not provide a range in which every individual effect must lie, and it is not a guarantee that the true effect is contained in this specific interval.

The registry does not describe the interval-construction method, whether any covariate adjustment was used, or whether the interval accounts for clustering by study center. It is therefore reasonable to describe the interval as shown, but not to claim that it reflects a particular modeling procedure that is absent from the record. In general, confidence intervals are useful because they show both direction and precision, whereas a p-value alone does not communicate the range of effects compatible with the data and method.

What does the p-value say?

The unadjusted p-value for the primary comparison is <0.001. In general, a p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. The term unadjusted indicates that this displayed p-value is not adjusted for multiple comparisons. The registry record does not state whether the sponsor used another prespecified inferential procedure for its main report.

The comparison data are consistent with a simple, unadjusted comparison of group means. The record does not provide enough detail to establish whether the sponsor's primary analysis used the same approach, whether baseline measurements entered the model, or how other design features were handled. The posted analysis listing contains no reported analyses, even though outcome summaries and comparison statistics are displayed. That distinction limits what can be inferred about the trial's full analysis plan.

Why can over-dispersion matter?

For a continuous outcome, over-dispersion is a general concern when observed variability is greater than the model assumes. If a method underestimates variability, its standard errors may be too small and its confidence intervals may be too narrow. If variability is modeled appropriately, uncertainty estimates better reflect the spread in the observations. The registry provides standard deviations for the group summaries, but it does not report a model diagnostic or an adjustment for over-dispersion. No conclusion about whether over-dispersion was present can be drawn from the record.

More broadly, the validity of an inferential result depends on assumptions about how observations were collected and analyzed. Randomization and masking describe important design features, but do not answer every analytical question. The record does not report the handling of repeated measurements, missing values, protocol deviations, or center-level correlation. These are not claims that the trial mishandled those issues; they are limits on what can be assessed from the registry entries.

What do the planning illustrations show?

The sample-size section uses the observed effect as a planning reference, then illustrates smaller fractions of that effect. It assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The listed values are participants per arm for this continuous endpoint. In general, power is the chance that a specified design would detect an effect of a specified size under the assumed model and testing procedure. These illustrations are not evidence about the original trial's design choices or the probability that the completed trial found a true effect.

The registry does not report the trial's original sample-size justification, its target power, or the assumptions used when planning enrollment. It also does not report interim analyses or a full statistical analysis plan. The sample-size calculations displayed alongside the outcome results should therefore be understood as separate planning illustrations, not as a reconstruction of the trial protocol. Statistical methods can describe uncertainty and support comparison, but they cannot replace missing design and analysis documentation.

11. Confidence Intervals and Precision

The primary confidence interval extends from -0.057 to -0.021 logMAR for the displayed mean difference. It is entirely below zero, so the estimated contrast is directionally consistent across the interval with a lower mean in the monofocal group under the comparison's arm ordering. The interval gives a range of effect sizes compatible with the procedure used to calculate it; it is not a range for individual participants' acuity measurements.

Precision concerns how narrowly the effect has been estimated. The interval does not collapse to a single value, so there is uncertainty about the exact size of the mean difference. At the same time, it does not include zero, which helps distinguish uncertainty about the magnitude from uncertainty about the direction relative to no difference. The p-value is also reported as <0.001, but the interval conveys more about the range of plausible mean differences than that thresholded p-value alone.

Interpretation still depends on the endpoint scale, its clinical context, and analysis details. The record does not report a clinically important difference threshold, a noninferiority margin, or the method used to construct the interval. It also does not report whether the analysis adjusted for other variables or study center. The confidence interval should therefore be read as the precision summary posted for this comparison, not as proof that all sources of uncertainty have been incorporated.

The group standard deviations and endpoint-specific sample counts provide context for the estimate, but they do not remove uncertainty about missing outcomes or the representativeness of the analyzed participants. Since the registry does not explain the relationship between the enrolled population and the primary endpoint counts, the effect's precision among those with posted endpoint data should not automatically be generalized to every enrolled subject. The interval quantifies statistical uncertainty as presented; it cannot address every limitation of design, conduct, or reporting.

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 table is a planning illustration based on the observed effect, not a report of the trial's original enrollment calculation. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The table gives participants per arm for this continuous endpoint. It does not give total events: event totals are relevant to time-to-event illustrations, whereas this comparison is based on a continuous measure.

The columns for 80% and 90% power describe hypothetical designs under the stated assumptions. In plain terms, 80% power is the chance of detecting the chosen effect at the specified significance level if that effect is the true one and the assumptions hold. The 90% column describes the corresponding chance under a design with the higher target probability of detection. These are design targets, not guarantees for an individual study and not probabilities that the observed finding is true.

The rows change the effect size used for planning: they consider the full observed effect, 75% of the observed effect, and 50% of the observed effect. As the effect assumed for planning becomes smaller, more participants are needed to detect it at the same power target. The table therefore illustrates how enrollment needs depend on the effect size a study aims to detect, as well as on the stated assumptions.

The registry does not report the original sample-size justification or the assumptions used to plan the completed trial. These displayed figures are not observed power. They should not be used to infer that the completed study was adequately or inadequately powered, since that judgment would require the original design target, analysis plan, and relevant 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.039; pooled standard deviation σ = 0.093.
2. n = 2 × (1.96 + 0.842)² × 0.093² / -0.039² = 89.8, rounded up to 90 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 <- -0.039                      # observed difference in means
sigma <- 0.0932705574573885                     # 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(3603600)
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 = 90 (80% power), 121 (90% power)
 75% of observed effect: n per arm = 160 (80% power), 214 (90% power)
 50% of observed effect: n per arm = 360 (80% power), 481 (90% power)
power.t.test: 90.8 
Simulated power at n = 90 per arm: 0.796 (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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, comparisons, time points, or analyses. In general, the more statistical tests considered, the greater the possibility that at least one will appear unusual by chance if no true effects exist. Researchers may address this by identifying a primary endpoint, specifying an order of testing, or adjusting significance thresholds or confidence intervals. The registry identifies a primary outcome and lists secondary outcomes, but a multiplicity adjustment or a formal testing hierarchy is not reported in the registry record.

The primary comparison is therefore distinct from the secondary comparisons. Its unadjusted p-value should not be interpreted as if it had been adjusted across every outcome in the study. Likewise, the secondary p-values are not a single confirmatory test of an overall treatment effect. The registry lists 13 outcome measures, which makes the absence of a reported multiplicity strategy relevant to interpreting the collection of results. This does not establish that no strategy existed elsewhere; it means the strategy is not reported in the registry record.

Missing data are another important issue for interpretation. The primary outcome summaries include 312 participants in the trifocal group and 156 in the monofocal group, while total enrollment is 501. The registry does not explain the relationship between those counts, or state how unavailable endpoint measurements were handled. It does not report whether the analysis used imputation, complete-case methods, sensitivity analyses, or another approach. No reason for missing measurements should be inferred from the difference between enrollment and endpoint counts.

The analysis population is also not described in sufficient detail. The registry does not say whether results are based on all randomized subjects, participants who received the assigned lens, or a defined subset satisfying other criteria. It does not report exclusions from analysis or protocol deviations. These details matter because estimates can be affected by which participants are included and how missing outcomes are handled.

Finally, the registry record does not report a detailed statistical analysis plan, interim analyses, or a full sponsor analysis narrative. It lists no reported analyses, despite displaying outcome summaries and comparison results. These omissions limit assessment of whether the analyses were prespecified and how the trial handled multiple outcomes and incomplete data. They do not, on their own, demonstrate that the conduct or analysis was inappropriate.

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: cerebrovascular accident (1.2%), chest pain (1.2%), ophthalmic herpes zoster (0.6%), cataract operation complication (0.6%), presyncope (0.6%).

The safety summary reports serious adverse events among 332 subjects at risk in the enVista MX60EF group and 169 subjects at risk in the enVista MX60E group. Serious adverse events affected 17 and 15 subjects, respectively. The registry also reports 3 deaths in the trifocal group and 1 in the monofocal group. These are group-level counts; they do not establish that a device caused an event or death.

The listed serious-event terms include Cerebrovascular accident and Chest pain, each shown as 1.2%, and Ophthalmic herpes zoster, Cataract operation complication, Presyncope, and Transient ischaemic attack, each shown as 0.6%. The record does not identify these terms as occurring in a particular group in the summary. The percentages should be read as displayed, without inferring additional denominators or recalculating event rates.

Safety counts are not directly comparable to the primary endpoint sample sizes without knowing how the safety populations and follow-up were defined. The registry does not provide event timing, individual case details, exposure-adjusted rates, or an attribution assessment in this summary. Serious events and deaths are important descriptive findings, but these registry counts alone cannot establish whether there is a causal difference between devices.

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

The primary result describes a difference in mean photopic monocular best-corrected distance visual acuity at the specified postoperative visit. The posted estimate and interval indicate that the two group means were not identical in the displayed comparison, with the monofocal group's mean lower on the logMAR scale. That is a statement about the measured endpoint and the reported analysis; it is not a conclusion about every aspect of vision or every participant's experience.

Statistical evidence and clinical importance are related but different. The unadjusted p-value is small, and the confidence interval lies below zero, but the registry does not state what size of logMAR difference patients or clinicians would consider important. Without such context, the statistical comparison cannot by itself establish the practical importance of the observed mean difference. Nor does a group average show how many participants had better, worse, or unchanged outcomes.

The result also does not show that one lens is preferable for every visual task. The secondary outcome summaries assess near and intermediate measures, and their direction differs from the primary distance acuity comparison. The primary endpoint is not a comprehensive measure of visual function, satisfaction, or quality of life. Safety summaries provide additional information, but event counts cannot establish causation or fully characterize comparative risk.

The completed randomized, double-masked design provides important context, but the registry does not report enough detail to resolve all questions about analysis populations, missing outcomes, multiplicity, or the statistical plan. The posted results should be read as registry summaries rather than a full account of trial conduct and analysis. They do not establish long-term outcomes beyond the stated assessment window, and they should not be used as individualized medical advice. A clinical decision would require broader evidence and patient-specific discussion; this page is a statistical interpretation of the record, not a recommendation.

17. Why This Trial Matters Statistically

This trial is statistically notable because it places a primary distance-acuity comparison in the context of randomized allocation and double masking, then reports both group summaries and an estimated mean difference. The estimate, confidence interval, and p-value each communicate a different aspect of the comparison: direction and size, uncertainty around the estimate, and compatibility with a null hypothesis under the method's assumptions. Reading them together is more informative than relying on any single statistic.

The record also illustrates why endpoint definition matters. The primary measure is monocular, best-corrected distance acuity, while the secondary summaries include binocular measures at near and intermediate distances. These are not redundant measurements. Their differing patterns show that conclusions about one visual task should not automatically be generalized to another. A well-defined primary endpoint helps orient interpretation, while secondary outcomes add breadth but raise multiplicity concerns.

There is also a useful distinction between study results and planning illustrations. The sample-size section explores hypothetical designs using fractions of the observed effect and specified assumptions. Those calculations can show how design requirements change when a target effect becomes smaller, but they do not reconstruct the original protocol. Keeping that distinction clear prevents a post-result planning exercise from being mistaken for evidence about the trial's original power.

Finally, the record demonstrates the value and limits of registry reporting. It makes key design features, outcome definitions, summary statistics, and selected safety counts accessible. At the same time, it does not report several details needed for a complete appraisal, including the analysis population, missing-data approach, multiplicity plan, and original sample-size justification. Statistical interpretation requires both attention to the reported estimates and candor about what the record leaves unresolved.

18. Limitations

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

The registry describes the design as randomized and double-masked but does not explain the randomization procedure, allocation concealment, or which roles were masked. It does not report details about how masking was maintained or assessed. These omissions make it difficult to evaluate implementation beyond the design labels.

The record gives total enrollment and endpoint-specific sample counts but does not explain why the counts differ or describe participant flow. It does not report reasons for missing endpoint measurements, the analysis population, or how missing data were handled. Those gaps restrict assessment of possible selection effects and of how well the analyzed participants represent all enrolled participants.

The registry does not report the original sample-size justification, a formal clinically meaningful threshold for BCDVA, or a noninferiority or superiority margin. The planning illustration is based on the observed effect and cannot answer whether the original design had adequate precision for a prespecified target. The record also does not provide a detailed statistical analysis plan, adjustment for multiple outcomes, interim-analysis details, or a description of adjustment for center effects.

Only some of the listed secondary outcomes have numeric summaries in the result details. The record does not provide a complete set of numeric results for every listed measure in those details. The available summaries may therefore not capture the full outcome picture. Moreover, unadjusted secondary comparisons should be treated cautiously when no multiplicity strategy is reported.

The safety information is presented as aggregate counts and selected event terms. It does not provide event timing, case-level descriptions, exposure-adjusted analyses, or causal attribution in this summary. These limitations do not show that any particular method was absent from the full trial process; they identify information not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluate the Safety and Effectiveness of the enVista® One-Piece Hydrophobic Acrylic Trifocal Intraocular Lens — NCT03603600.
• Registry record last updated 2024-12-24; status last verified 2024-12.
• Results first posted 2024-12-24.
• 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

The record describes a completed, prospective, multicenter, randomized, double-masked, parallel-group, active-controlled study of two intraocular lenses in subjects undergoing cataract extraction. The devices were enVista MX60EF, a trifocal multifocal lens, and enVista MX60E, a monofocal lens. The listed enrollment is 501.

The primary outcome was mean photopic monocular best-corrected distance visual acuity in logMAR at Post-Operative Visit 4. The posted comparison reports a mean difference of -0.039, with a confidence interval from -0.057 to -0.021 and an unadjusted p-value of <0.001. Secondary summaries cover selected binocular near and intermediate outcomes, while aggregate serious adverse event and death counts are also reported.

The registry does not report the original sample-size justification, detailed analysis plan, multiplicity approach, missing-data handling, or a complete explanation of analysis populations. These gaps constrain interpretation of the posted results and safety summaries.