Evaluate Efficacy and Safety of POS to Improve Distance-corrected Near Visual in Participants With Presbyopia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluate Efficacy and Safety of POS to Improve Distance-corrected Near Visual in Participants With Presbyopia (NCT06542497), a randomized phase 3 study. The primary outcome is Percentage of Subjects With ≥ 15 Letters of Improvement in Binocular DCNVA and With < 5 Letters of Loss in Binocular BCDVA From Baseline Comparing POS-treated Participants to Placebo-treated Participants at 12 Hours Post-dose at Visit 4 (Day 8).

2. Clinical Question

3. Trial Design

NCT06542497 is registered as a completed phase 3 trial of POS in participants with presbyopia. The study start date is 2024-08-15, and the primary completion date is 2025-04-03. The registry records 569 participants enrolled. The official title describes the study as randomized, double-masked, placebo-controlled, and multicenter; the design fields classify it as randomized, triple-masked, and parallel. The difference between the title's masking description and the masking field is present in the registry record; further explanation is not reported.

The intervention arms were 0.75% phentolamine ophthalmic solution and phentolamine ophthalmic solution vehicle. The latter is identified as placebo. The primary endpoint compares the arms at 12 hours post-dose at Visit 4 (Day 8), using a combined binocular near- and distance-vision response. The registry lists the outcome unit as participants and the measure as a count of participants.

The registry record gives an efficacy-arm count of 338 for POS and 226 for placebo in the primary result. These are the posted denominators for that result; the record does not explain how the analysis population was defined or why those counts differ from the enrollment figure. Safety results use different arm denominators, which are described with the safety findings. Allocation concealment, the randomization sequence method, and the original sample-size justification are not reported in the registry record. The record also does not state the trial's original target allocation ratio.

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

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 Percentage of Subjects With ≥ 15 Letters of Improvement in Binocular DCNVA and With < 5 Letters of Loss in Binocular BCDVA From Baseline Comparing POS-treated Participants to Placebo-treated Participants at 12 Hours Post-dose at Visit 4 (Day 8), measured over 8 Days.

The primary endpoint is the percentage of participants who satisfy two criteria together at 12 hours post-dose at Visit 4 (Day 8). From baseline, binocular DCNVA must improve by at least 15 letters, while binocular BCDVA must lose fewer than 5 letters. The registry records the outcome as a count of participants, with posted counts of 92 in the POS arm and 26 in the placebo arm.

Combining the two criteria makes the endpoint more specific than measuring near-vision change alone: a participant must meet the near-vision improvement threshold and remain within the stated limit for loss in the distance-vision measure. This can be useful when an intervention is evaluated on a target function while a second visual measure is included in the same response definition. The outcome is nevertheless a threshold-based summary. It does not show the size of improvement among responders, the distribution of changes among all participants, or results at other times.

The endpoint's wording refers to percentages, but the posted arm values are counts. The comparative recalculation therefore expresses the difference in response probability on a proportion scale. The record does not provide a separate explanation of how missing observations, participants who did not complete the visit, or borderline measurements were handled for this endpoint.

7. Results Posted in the Registry

• 0.75% Phentolamine Ophthalmic Solution: 27.2% (92/338) versus 11.5% (26/226) on control; risk difference 15.7 percentage points (95% CI 9.4 to 22.0), risk ratio 2.37 (1.58–3.53); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because it classifies each participant according to whether both threshold conditions are met. Binary outcomes are commonly summarized by the number meeting the definition and the number assessed in each group. Here the registry posts 92 participants meeting the endpoint among 338 in the POS arm and 26 among 226 in the placebo arm. Those counts retain the outcome's direct clinical definition, while comparative statistics provide ways to quantify the difference between arms.

What does the risk difference mean?

The risk difference is the response proportion in one arm minus the response proportion in the other, with the comparison oriented as POS versus placebo. The recalculated estimate is 0.157. This is an absolute contrast on the proportion scale, not a relative multiplier. An absolute measure is often straightforward to interpret because it describes how much the estimated response probability differs between groups. The estimate is unadjusted: it comes from the posted arm-level counts rather than a model that accounts for participant-level covariates.

A confidence interval accompanies the risk-difference estimate, from 0.094 to 0.220. In general, a confidence interval communicates the range of effect estimates reasonably compatible with the observed data under the calculation's assumptions. A narrower interval indicates greater precision than a wider interval, but an interval does not remove uncertainty or account for sources of bias not represented in the calculation. The confidence level is not reported for the posted recalculation.

How do relative measures differ?

The recalculation also gives a risk ratio of 2.366, with a confidence interval from 1.584 to 3.535, and an odds ratio of 2.877, with a confidence interval from 1.791 to 4.62. A risk ratio compares the response proportions as a ratio; an odds ratio compares the odds of response. These are relative measures, whereas the risk difference is absolute. Relative measures can sound large even when the underlying absolute contrast is more modest, so interpretation should consider the outcome frequency and the absolute estimate as well. The odds ratio is not interchangeable with the risk ratio, particularly when an outcome is not rare.

Why use logistic regression?

Logistic regression is a standard approach for modeling a binary outcome. It models the odds of the outcome and can be used to test a group comparison; depending on the specified model, it can also account for covariates. The registry reports a logistic-regression superiority analysis with p < 0.001, but does not provide a model coefficient, confidence interval, covariates, or detailed specification. It is therefore possible to identify the method and reported test result, but not to reconstruct the sponsor's full model from the registry entry.

What does the p-value address?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the model assumptions. It is not the probability that the null hypothesis is true, and it does not tell how likely the result is to recur. The recalculated p-value is unadjusted and is reported as <0.001. The registry's logistic-regression p-value is < 0.001. Because the methods differ, the two values need not match. Neither p-value describes the magnitude or practical importance of the estimated difference.

Why can binary outcomes be less informative than measurements?

Turning a continuous change into a responder/nonresponder classification can make an endpoint easier to communicate, but it discards information about the degree of change. Participants just short of the threshold are classified with those with little or no improvement, while participants who cross the threshold are grouped together even if their changes differ. The combined near- and distance-vision criteria add a second condition, so the result represents the share meeting the full rule rather than an average change on either measure. The registry lists secondary outcomes that include letter-change measures, response thresholds, visual-acuity cutoffs, and assessment times, but numerical results for those outcomes are not part of the registry entries available for this interpretation.

Why do analysis details matter?

Randomization can support a fair comparison by allocating participants to study groups, but the interpretation also depends on what participants were analyzed, how missing values were treated, whether the planned model was followed, and whether multiple outcomes were considered. Those details are not reported in the registry record. The unadjusted recalculation is useful as a transparent comparison of posted counts, but it is not a replacement for the sponsor's model or for information about the full statistical plan.

10. Confidence Intervals and Precision

The unadjusted risk-difference estimate is 0.157, with a confidence interval from 0.094 to 0.220. The interval communicates uncertainty around the estimated absolute difference in the proportions meeting the combined response definition. Its width reflects sampling variation under the calculation's assumptions; it does not account for unreported design features, missing-data decisions, or bias.

The interval endpoints are above zero. In the setting of this unadjusted calculation, that indicates that the range of estimates compatible with the data is positive. It does not mean that every possible analysis or every population would produce the same result. Nor does it establish the importance of the difference for participants. The record does not report the confidence level or a clinically important threshold for interpreting the risk difference.

The relative estimates also have uncertainty intervals: the risk ratio is 2.366, with a confidence interval from 1.584 to 3.535, and the odds ratio is 2.877, with a confidence interval from 1.791 to 4.62. These intervals are on different scales from the risk-difference interval and should not be compared by their numerical widths. The registry's logistic-regression result does not include a coefficient or confidence interval, so the precision of that modeled estimate cannot be assessed from the reported analysis entry.

Precision concerns how tightly an effect is estimated, not whether a result is free from uncertainty. A confidence interval summarizes statistical uncertainty conditional on a method and its assumptions; it does not incorporate all uncertainty about endpoint selection, trial conduct, missing observations, or the generalizability of the findings. The registry record does not report enough detail to evaluate those issues fully.

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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect, with a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at 100%, 75%, or 50% of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

For planning at 100% of the observed effect, the estimates are 99 participants per arm for 80% power and 131 participants per arm for 90% power. At 75% of the observed effect, the estimates are 162 participants per arm for 80% power and 216 participants per arm for 90% power. At 50% of the observed effect, the estimates are 331 participants per arm for 80% power and 443 participants per arm for 90% power.

In plain language, 80% power is the assumed chance of detecting an effect of the specified size under the planning model if that effect is present; 90% power uses a higher detection target and therefore requires more participants under these assumptions. The results illustrate that smaller effects need more participants to detect. These figures are planning illustrations, not observed power.

The estimates depend on the observed effect serving as the starting point and on the stated model assumptions. If the true effect differs from the observed estimate, or if the design, allocation, outcome frequency, or analysis differs from these assumptions, the required sample size could differ. The original rationale for the trial's enrollment is not reported in the registry record, so these illustrations should not be taken as evidence about the design decisions made for the trial.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.115; treatment proportion p₁ = 0.272; average p̄ = 0.194.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5588 = 1.0952.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5476 = 0.4609.
4. n = (1.0952 + 0.4609)² / (0.1571)² = 98.1, rounded up to 99 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.115044247787611                          # control proportion
p1 <- 0.272189349112426                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(6542497)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 99 (80% power), 131 (90% power)
 75% of observed effect: n per arm = 162 (80% power), 216 (90% power)
 50% of observed effect: n per arm = 331 (80% power), 443 (90% power)
power.prop.test: 98.1 
Simulated power at n = 99 per arm: 0.814 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports the sponsor's primary superiority analysis as logistic regression, with p < 0.001. It does not report the model estimate, confidence interval, adjustment variables, or full specification. The sponsor analysis is therefore identifiable by method and test result, but its estimated effect and precision cannot be compared numerically in full with the recalculation.

The recalculation uses the posted arm-level counts and is an unadjusted risk-difference analysis. It estimates a difference of 0.157, with a confidence interval from 0.094 to 0.220, and gives an unadjusted p-value of <0.001. The registry record does not flag a discrepancy between its reported analysis and the recalculation. The different p-values are expected to be not identical when the analyses use different methods and may use different model assumptions; the registry does not provide details sufficient to explain their exact relationship.

The sponsor's logistic-regression result is the reported trial analysis and should be distinguished from the summary-statistic recalculation. The recalculation offers a transparent, unadjusted contrast of the posted counts, not a reproduction of the sponsor's full model. Neither result alone addresses the unreported analysis population, missing-data approach, or multiplicity strategy.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 19 outcome measures and records 18 secondary outcomes as posted. The secondary outcomes span several near-vision response thresholds, binocular and monocular assessments, letter changes, visual-acuity cutoffs, and time points including Day 1, Day 3, Day 8, and Week 6. Considering multiple outcomes and time points creates a multiplicity issue: when many statistical tests are performed, the chance of at least one small p-value under a collection of null hypotheses can increase. Whether and how the trial addressed multiplicity is not reported in the registry record.

The registry gives one sponsor-reported primary superiority p-value, but the statistical plan, hierarchy of secondary endpoints, and any adjustment procedure are not reported. The number of analyses listed in the record is 40. Without the planned testing strategy, it is not possible to determine whether the reported primary test was the only confirmatory comparison, how secondary results should be interpreted, or whether any adjustment was intended.

Handling of missing data is also not reported in the registry record. The available entry does not explain whether all randomized participants were included, how unavailable Day 8 measurements were handled, whether participants who discontinued were counted as nonresponders, or whether any imputation method was used. These choices can affect a binary endpoint because the response classification requires measurements on both near and distance vision.

The analysis population is not described in enough detail to identify whether the primary analysis followed an intention-to-treat principle, a per-protocol approach, or another definition. The efficacy denominators are 338 for POS and 226 for placebo, while the safety denominators are 341 and 228. The record does not explain the differences among enrollment and these analysis denominators. Interim analyses and any associated decision rules are not reported in the registry record. Consequently, the posted result can be interpreted at the level of the registered endpoint and reported analysis, but important features of the confirmatory statistical plan remain 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: encephalitis bacterial (0.4%), rib fracture (0.4%), acute respiratory failure (0.4%), intracranial aneurysm (0.4%), retinal vein occlusion (0.3%).

The safety record lists serious adverse events among 341 participants at risk in the POS group and 228 at risk in the placebo group. It records 4 participants with serious adverse events in the POS group and 3 in the placebo group. Deaths are recorded as 0 in each group. Other adverse events are recorded for 158 participants in the POS group and 21 in the placebo group, with the same safety denominators of 341 and 228 respectively. These are counts from the registry, not comparative estimates adjusted for exposure or other factors.

The serious-event terms listed include encephalitis bacterial, rib fracture, acute respiratory failure, and intracranial aneurysm, each at 0.4%; retinal vein occlusion and cholecystitis, each at 0.3%. The registry lists these as serious-event terms, but the record details do not provide event counts for each term or explain whether terms can occur in the same participant. Percentages should be read as the posted figures, not as evidence of a causal relationship to study treatment.

These summaries do not establish whether an event was caused by an intervention. The registry entries do not provide event timing, exposure-adjusted rates, severity breakdowns beyond the serious-event category, or details of how events were adjudicated. The figures describe the recorded safety counts in the stated groups and should not be read as a complete comparative safety assessment.

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

The posted primary result concerns a narrowly defined response at one assessment: at 12 hours post-dose on Day 8, a participant had to meet both the near-vision improvement threshold and the distance-vision loss limit. The counts were 92 among 338 in the POS arm and 26 among 226 in the placebo arm. The unadjusted risk-difference estimate was 0.157, with a confidence interval from 0.094 to 0.220. The sponsor-reported logistic-regression superiority test had p < 0.001.

Statistically, the findings indicate a higher estimated proportion meeting this combined response definition in the POS group than in the placebo group in the reported comparison. They do not show the average magnitude of near-vision change, the full distribution of individual changes, or whether the result persists at every time point. The response threshold also groups participants who meet the criteria together, even if their measured changes differ.

The result is not, by itself, a comprehensive statement about visual function, daily activities, durability, or safety. The registry lists secondary outcomes that could address other thresholds and assessment times, but their numerical findings are not included in the record details. The safety counts provide descriptive information, but they do not establish causation or replace a detailed assessment of event timing and exposure.

Statistical significance is distinct from clinical importance. The registry does not report a clinically important difference threshold for the primary response proportion, so the practical importance of the estimated difference cannot be determined from the p-value alone. Generalization is also limited to the study population, intervention, comparator, endpoint, and assessment conditions described in the record. Details about the enrolled participants beyond presbyopia, missing-data handling, and the analysis population are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates several issues that matter when interpreting a clinical comparison with a binary primary outcome. First, the endpoint combines two visual criteria: a minimum improvement in binocular DCNVA and a limit on loss in binocular BCDVA. That definition makes clear what qualifies as a response, but it also means the summary does not convey the amount of change for each participant or the separate behavior of the two measurements.

Second, absolute and relative measures tell different parts of the statistical story. The unadjusted risk difference is 0.157, while the risk ratio is 2.366 and the odds ratio is 2.877. The absolute difference describes the contrast in response proportions; the relative measures express that contrast in ratio form. Reading them together helps avoid treating a relative effect as if it directly conveyed the absolute amount of change.

Third, the registry includes both a sponsor-reported logistic-regression test and an unadjusted recalculation from posted counts. Their methods and reported p-values differ, and the model details are incomplete. This underscores why a p-value should not be interpreted without knowing what was modeled and how the analysis was defined. The registry also lists many outcomes and analyses, while the multiplicity approach is not reported.

Finally, planning illustrations based on an observed effect depend on assumptions and should not be confused with the trial's original design rationale or an assessment of observed power. The record's missing-data approach and analysis population are also not reported. Together, these features show why effect size, precision, outcome definition, and statistical-plan transparency are all relevant to interpreting a registered trial result.

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 record does not report the sponsor's logistic-regression estimate or confidence interval, the model covariates, or enough detail to reproduce that analysis. The unadjusted recalculation is based on posted arm-level counts and cannot substitute for the full model. The confidence level for the recalculated intervals is not stated in the record details.

The analysis population and missing-data procedures are not reported. The primary efficacy counts use denominators of 338 and 226, whereas the safety counts use denominators of 341 and 228; the reasons for the differences are not explained. The original sample-size justification and design assumptions are also not reported, so the planning illustrations based on the observed effect cannot be treated as the trial's design rationale.

The registry lists 19 outcome measures and 40 analyses, but does not report a multiplicity strategy, endpoint hierarchy, or interim-analysis plan. This limits assessment of how the primary and secondary findings were intended to be interpreted together. Although secondary outcome descriptions include other assessment times and measures, their numerical results are not included in the registry record for this analysis.

The masking information is not fully consistent across registry fields: the official title says double-masked, while the design field says triple-masked. The record does not explain this difference. Additional limitations include the threshold-based nature of the primary outcome, which does not summarize the magnitude or distribution of visual changes, and the lack of reported clinical-importance criteria. These limitations constrain interpretation to the specific posted comparison and do not resolve broader questions about generalizability or the overall benefit-risk profile.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluate Efficacy and Safety of POS to Improve Distance-corrected Near Visual in Participants With Presbyopia — NCT06542497.
• Registry record last updated 2026-10-26; status last verified 2026-10.
• Results first posted 2026-08-17.
• 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

NCT06542497 is a completed phase 3 randomized, parallel-group study of 0.75% phentolamine ophthalmic solution versus phentolamine ophthalmic solution vehicle in participants with presbyopia. The primary endpoint is a combined binocular response at 12 hours post-dose at Visit 4 (Day 8): at least 15 letters of DCNVA improvement from baseline and fewer than 5 letters of BCDVA loss. The registry reports 92 participants meeting the response definition among 338 in the POS arm and 26 among 226 in the placebo arm.

The unadjusted recalculation estimates a risk difference of 0.157, with a confidence interval from 0.094 to 0.220 and p < 0.001. The registry reports a logistic-regression superiority analysis with p < 0.001. The record lists 18 secondary outcomes, but the numerical results for them are not reported in the registry record details used for this interpretation. Missing-data handling, analysis populations, multiplicity procedures, and the original sample-size rationale are not reported.