An Evaluation of the Efficacy and Safety of CSF-1 in the Temporary Correction of Presbyopia (NEAR-2): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Evaluation of the Efficacy and Safety of CSF-1 in the Temporary Correction of Presbyopia (NEAR-2) (NCT04599972), a randomized phase 3 study. The primary outcome is Percentage of Subjects With a ≥ 3-line Gain in BDCVA (Best Distance-Corrected Visual Acuity) at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8, 1 Hour Post-Dose 1..

2. Clinical Question

3. Trial Design

NEAR-2 was a Phase 3, randomized, double-masked, vehicle-controlled, parallel-group study of CSF-1 for temporary correction of presbyopia. The sponsor was Orasis Pharmaceuticals Ltd. The registry lists enrollment of 304 and a four-visit, multi-center study. Study status is completed; the recorded start was 2020-10-26 and primary completion was 2022-01-21. The registry describes the treatment period as approximately 2 weeks.

Participants were assigned to CSF-1 or vehicle. Both regimens were one drop in both eyes twice daily for approximately 2 weeks. Double masking means the study was designed so that treatment assignment was concealed from participants and relevant study personnel, but details about who remained masked and how masking was maintained are not reported in the registry record. The allocation method is recorded as randomized; details of sequence generation and concealment are not reported.

The primary outcome was a binary responder measure assessed on Day 8, one hour after the first dose. The full analysis set included randomized participants who received at least one dose, with analysis according to randomized assignment. The reported arm counts for this endpoint were 64 responders among 154 in the CSF-1 group and 32 among 150 in the vehicle group. Safety figures use different at-risk counts, which are described separately in the safety discussion.

The registry record does not report the trial's original sample-size justification, detailed eligibility criteria, allocation concealment procedures, adherence summaries, or a full statistical analysis plan. It also does not describe whether or how interim analyses were conducted. These details should not be inferred from the design label or from the completed status.

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:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): included all randomized subjects who received at least 1 dose of the study drug. Subjects in the FAS were analyzed as randomized.

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 a ≥ 3-line Gain in BDCVA (Best Distance-Corrected Visual Acuity) at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8, 1 Hour Post-Dose 1., measured over Baseline (Day 1) to Day 8 (1 hour post-Dose 1).

The primary endpoint counts participants meeting a prespecified responder definition on Day 8, one hour after the first dose. A responder had to achieve a gain of at least 3 lines in best distance-corrected visual acuity at 40cm and have no loss of 5 or more letters in that measure at 4m. In practical statistical terms, this is a binary outcome: each participant either meets both parts of the definition or does not.

The endpoint is intended to capture near-vision improvement while imposing a condition on distance-corrected acuity. Using a combined definition makes the result more specific than counting near-vision gain alone. It also means the result depends on both thresholds and on the assessment time. It does not measure the size of improvement beyond the threshold, how long an individual response lasts, or broader everyday functioning.

The registry describes the primary measure as the number of participants who were responders and gives the full analysis set as the population. Although the title calls the result a percentage, the posted arm results are counts with group denominators. The primary time point is not interchangeable with other Day 8 assessments: the secondary outcomes include measurements after later doses and at different post-dose times. The registry record does not report additional details about endpoint adjudication, handling of repeated measurements, or missing primary assessments.

7. Results Posted in the Registry

• CSF-1: 41.6% (64/154) versus 21.3% (32/150) on control; risk difference 20.2 percentage points (95% CI 10.0 to 30.4), risk ratio 1.95 (1.36–2.79); unadjusted two-proportion 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.

Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CSF-1: 40.3% (62/154) versus 20.7% (31/150) on control; risk difference 19.6 percentage points (95% CI 9.5 to 29.7), risk ratio 1.95 (1.35–2.81); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for CSF-1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8 at 1 Hour Post-Dose 2

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CSF-1: 51.9% (80/154) versus 16.7% (25/150) on control; risk difference 35.3 percentage points (95% CI 25.4 to 45.2), risk ratio 3.12 (2.11–4.60); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for CSF-1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8 at 2 Hours Post-dose 2

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CSF-1: 46.1% (71/154) versus 19.3% (29/150) on control; risk difference 26.8 percentage points (95% CI 16.7 to 36.9), risk ratio 2.38 (1.65–3.45); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for CSF-1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The three secondary outcomes use the same general responder definition at different Day 8 post-dose assessment times. Across these secondary comparisons, the observed direction is consistent with the primary result: the reported responder outcomes favor CSF-1 relative to vehicle. The sponsor's logistic regression analyses for the secondary outcomes are each labelled superiority, with p < 0.01. These analyses add context about related assessments but are not separate tests of unrelated outcomes.

The secondary measures relate to the primary endpoint through their shared visual-acuity thresholds and responder classification. Their differing assessment times mean they address different points in the dosing schedule. Agreement in direction can make the overall pattern more coherent, but it does not establish persistence beyond the measured times or resolve limitations in the primary endpoint. Nor should multiple related assessments be treated as independent replications of the primary finding.

The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary hypotheses. General statistical explanation: when several outcomes are tested, the chance of at least one small p-value can rise if each result is judged separately without accounting for the family of tests. Thus, unadjusted secondary results generally carry less weight than a prespecified primary result. They can be informative as supportive findings, while their evidential strength depends on the analysis plan and the full set of outcomes examined, details that are not reported in the registry record.

The record lists three secondary outcomes and four analyses overall, alongside the primary result. It does not report whether additional outcomes were collected but not posted, or how the secondary analyses were prioritized. The secondary pattern should therefore be read as consistency within the reported outcomes, not as proof that every relevant endpoint or time point would produce the same result.

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

• Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m.
• Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8 at 1 Hour Post-Dose 2
• Percentage of Subjects With a ≥ 3-line Gain in BDCVA at 40cm and no Loss in BDCVA ≥ 5 Letters at 4m on Day 8 at 2 Hours Post-dose 2

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because the responder definition classifies each participant as meeting or not meeting a combined threshold. For a binary outcome, a group proportion describes the share of participants with the event of interest. The posted primary counts are 64 of 154 for CSF-1 and 32 of 150 for vehicle. A risk difference expresses the difference between those proportions, while a risk ratio compares one proportion with the other. These are distinct measures and answer related but non-identical questions.

What does the sponsor's odds ratio describe?

The sponsor used logistic regression and reported an odds ratio. Odds are the probability of an event divided by the probability of no event; an odds ratio compares those odds across groups. It is not the same quantity as a risk difference or risk ratio, and it can be less intuitive than a direct comparison of proportions. The registry gives the sponsor's odds ratio as 2.979, with a 95% confidence interval from 1.753 to 5.064 and p < 0.01. The registry record does not report the model covariates, so the extent and nature of any adjustment cannot be described.

A confidence interval gives a range of estimates compatible with the data and the statistical procedure, under its assumptions. It conveys uncertainty in the estimated association; it is not a range containing a known treatment effect with certainty. For an odds ratio, a value of one represents equal odds in the groups. The reported interval lies above that reference. A p-value measures how incompatible the data are with a specified null model, assuming that model and the analysis conditions hold. It does not measure the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect.

Why distinguish the posted recalculation from the reported analysis?

The recalculated comparison is an unadjusted calculation from the aggregate counts in the registry. The sponsor's result is from logistic regression. Differences can arise because a regression model may account for variables or structures that a simple comparison of totals does not. Since the record flags a discrepancy and does not provide enough model detail to reproduce the sponsor analysis, the sponsor's reported analysis takes precedence as the trial's own inferential result. The simple recalculation should be understood as a separate summary, not as a correction of the sponsor's finding.

Randomization is intended to make treatment groups comparable on average, but it does not guarantee that every observed characteristic is balanced. The registry's allocation label establishes that the study was randomized; it does not provide sequence-generation or concealment details. Likewise, masking can reduce some opportunities for expectations to influence reporting or assessment, but the available record does not describe masking procedures or whether masking was successful.

What does the analysis population mean?

The stated full analysis set includes randomized participants who received at least one dose, analyzed as randomized. This preserves the randomized assignment for those included, rather than reclassifying them according to treatment received. It is not identical to an analysis of every randomized participant if someone did not receive a dose. The registry does not report how many randomized participants, if any, were excluded from the full analysis set or the reasons for any exclusions. Missing-outcome handling is also not reported.

The outcome is assessed at a defined time, rather than being a time-to-event outcome. General statistical explanation: for binary outcomes, the observed proportion can be affected by the threshold definition, assessment timing, missing measurements, and the population included in the analysis. A narrow endpoint definition can make the event easier to interpret but does not capture all dimensions of response.

How should the secondary analyses be read?

The registry reports three secondary responder measures, each assessed at a different Day 8 time relative to dosing. The sponsor reports logistic regression odds ratios for these comparisons as well. They are repeated assessments of a related endpoint, not wholly independent confirmations. The registry does not report a multiplicity plan, such as a procedure controlling the chance of false-positive findings across the primary and secondary outcomes. General statistical explanation: when several hypotheses are tested, interpreting every unadjusted p-value as if it were the only test can overstate the strength of evidence. For this reason, secondary results are best treated as supporting context rather than as equivalent to the primary analysis.

In general, statistical methods should be interpreted together with their assumptions, outcome definitions, analysis population, and missing-data approach. The registry record includes some of these elements, including the primary definition and full analysis set, but the original statistical plan, sample-size justification, model covariates, and missing-data procedures are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor's primary odds ratio is 2.979, with a 95% confidence interval from 1.753 to 5.064. This interval communicates uncertainty in the estimated odds comparison under the logistic regression method. Its endpoints are both above the null value of one, which aligns with the reported p < 0.01. The interval is not a guarantee that the true effect lies within its bounds, nor does it describe the range of individual participant outcomes.

Precision is different from statistical significance. An estimate can be statistically distinguishable from a null value yet still leave uncertainty about the magnitude of an effect. The width of an interval reflects information in the data and the analysis, while interpretation also depends on whether the measure is clinically meaningful. Here, the odds ratio is not itself a probability difference, so it should not be read as saying that the chance of response is multiplied by that value.

The simple unadjusted recalculation is based on the posted counts, whereas the sponsor interval comes from logistic regression. Because the registry flags a discrepancy and does not give sufficient model detail for reproduction, the sponsor analysis takes precedence for the reported trial inference. The interval for the recalculation should not be conflated with the sponsor's interval.

All estimates are tied to the endpoint definition, analysis population, and Day 8 assessment time. The registry does not report detailed missing-data methods or a fuller account of model assumptions, which limits independent evaluation of precision. Confidence intervals quantify statistical uncertainty under an analysis; they do not cover every source of uncertainty, such as limitations in outcome choice, generalizability, or unreported design details.

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 planning figures are participants per arm for these binary responder outcomes, not total events. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It sets the effect to detect as the stated fraction of the observed effect. These are planning assumptions for an illustration based on the observed result, not the trial's original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the approximate participants per arm required under those assumptions for an analysis to have an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm. For example, the primary endpoint's illustration lists 82 participants per arm for planning around 100% of the observed effect and 298 participants per arm for planning around 50% of the observed effect at 80% power. The corresponding 90% planning figures are 109 and 398 participants per arm.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm. The displayed figures vary across endpoints because the observed effects and event patterns vary. They are not a record of the actual enrollment decision and do not demonstrate that the completed study had a specified probability of success. This is not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.213; treatment proportion p₁ = 0.416; average p̄ = 0.314.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6566 = 1.2870.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6409 = 0.5394.
4. n = (1.2870 + 0.5394)² / (0.2023)² = 81.5, rounded up to 82 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 <- 0.213333333333333                          # control proportion
p1 <- 0.415584415584416                          # 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(4599972)
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 = 82 (80% power), 109 (90% power)
 75% of observed effect: n per arm = 140 (80% power), 186 (90% power)
 50% of observed effect: n per arm = 298 (80% power), 398 (90% power)
power.prop.test: 81.5 
Simulated power at n = 82 per arm: 0.804 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor's primary analysis is logistic regression, reporting an odds ratio of 2.979 with a 95% confidence interval from 1.753 to 5.064 and p < 0.01. The registry labels this analysis as superiority. It is the sponsor's model-based result and should be distinguished from a simple comparison recalculated from the posted responder counts.

The recalculation uses only aggregate group counts and produces an unadjusted comparison. The registry identifies a discrepancy between that result and the sponsor's analysis. The model details needed to reproduce the regression result, including any covariates, are not reported in the registry record. As a result, the recalculation cannot establish that the sponsor analysis is wrong or explain the source of the difference. The sponsor's own analysis takes precedence for the trial's reported inference.

This distinction is about methods, not a reason to ignore the underlying counts. Counts describe what was posted for each group; regression estimates a comparison using a specified model. The two can differ without being the same estimand or using identical assumptions. Readers should retain the measure label when interpreting the estimate: the sponsor reports an odds ratio, not a risk difference. The registry does not provide further detail about model diagnostics or covariate selection.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and three secondary endpoints, with four analyses overall. It does not report whether the trial used a multiplicity adjustment, a hierarchy for testing outcomes, or another prespecified strategy for controlling false-positive risk across analyses. This absence does not show that no such plan existed; it means the approach is not reported in the registry record.

General statistical explanation: if multiple hypotheses are tested, the chance of at least one result appearing unusually strong by chance can increase when each test is interpreted in isolation. Adjustments or a prespecified testing sequence can address that issue, but their use and details cannot be assumed. The primary result and secondary results should therefore not all be treated as having identical evidential status. The primary outcome is the central comparison; the secondary outcomes offer supporting information that needs more cautious interpretation in the absence of a reported multiplicity plan.

The stated full analysis set consists of randomized participants who received at least one dose and were analyzed according to randomized assignment. That definition clarifies the intended population for the primary analysis, but the record does not report a detailed account of exclusions from that set. It also does not report how missing outcome measurements were handled, whether any imputation was used, or what sensitivity analyses assessed the effect of missing data. These omissions limit evaluation of whether missingness could have influenced the responder comparisons.

The record also does not report the original statistical analysis plan, the sample-size justification, or whether interim analyses were conducted. These details matter for understanding which outcomes and methods were prespecified and how the final interpretation was controlled. They should be treated as unreported rather than inferred from the posted analyses or the completed study status.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infective arthritis (0.7%).

The registry reports serious adverse events among 153 participants at risk in the CSF-1 group and 151 at risk in the vehicle group. The serious adverse event counts were 0 for CSF-1 and 1 for vehicle. The registry lists no deaths in either group. Infective arthritis is listed among the top serious event terms at 0.7%; the record does not establish a causal relationship between that event and either study product.

For other adverse events, the registry reports 35 affected participants among 153 at risk in the CSF-1 group and 2 among 151 at risk in the vehicle group. These figures are counts of participants recorded as affected, and should be distinguished from the serious-event counts. The at-risk denominators differ from the primary full analysis set denominators, so they should not be substituted for the primary efficacy denominators.

These registry figures describe reported events in this study; they do not by themselves determine causality, severity beyond the serious-event classification, or comparative safety across broader populations. The record does not provide event-level timing, duration, or additional attribution details in the registry record reported.

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

The posted primary results show more participants meeting the defined responder threshold in the CSF-1 group than in the vehicle group at the specified Day 8 assessment. The sponsor's logistic regression analysis reports an odds ratio of 2.979, a 95% confidence interval from 1.753 to 5.064, and p < 0.01. This supports a statistical difference under the sponsor's reported model and outcome definition. The registry also identifies a discrepancy with the simple unadjusted recalculation, so the sponsor's analysis takes precedence for the trial's reported inference.

The finding applies to the study population, treatment schedule, endpoint criteria, and assessment time recorded. It does not establish how long a response lasts, whether it translates into improved everyday functioning, or how the endpoint relates to outcomes important to each individual. The responder threshold also simplifies a continuous visual-acuity measure into a yes-or-no classification; participants who fall on either side of the threshold may have more similar underlying measurements than that classification suggests.

The result should not be interpreted as a complete account of harms. The registry reports serious and other adverse event counts, but those figures alone do not explain event causes or capture every aspect of safety. In addition, missing-data methods, multiplicity handling, and several design and analysis details are not reported in the registry record.

Statistical evidence is one part of interpreting a clinical trial. The confidence interval describes uncertainty for the odds comparison under the reported analysis, while generalizability and practical importance depend on the population, outcome, duration, and context. The registry record does not support conclusions beyond the outcomes and conditions it reports.

18. Why This Trial Matters Statistically

NEAR-2 illustrates why a clinical result should be read through its endpoint definition and analysis method, rather than through a headline estimate alone. The primary measure is a binary responder classification combining near-vision gain with a condition on distance-corrected acuity. That makes the criterion interpretable as a threshold, while also limiting what the result says about the range of visual changes within each group.

The registry presents both group counts and a sponsor logistic regression analysis. Those summaries answer related questions but are not interchangeable: counts describe the observed outcomes, while an odds ratio expresses a model-based comparison on the odds scale. The registry flags a discrepancy with a simple recalculation, making it especially important to distinguish the sponsor's reported analysis from an unadjusted calculation and to give precedence to the sponsor result for its inferential claim.

The related secondary assessments show a consistent direction, but repeated related outcomes raise questions about multiplicity and how evidence is weighted. Since the registry does not report the multiplicity strategy, secondary findings merit a more cautious role than the primary comparison. Similarly, the stated full analysis set gives useful information about who was analyzed, while unreported missing-data handling and model details leave uncertainty about independent reproducibility.

Finally, the planning illustration demonstrates how assumptions about the target effect and desired power shape sample-size requirements. It is not a substitute for the trial's original design rationale, which is not reported in the registry record. Together, these features make the study a useful example of separating observed counts, model-based inference, planning calculations, and limitations in a registry summary.

19. Limitations

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

The registry record does not report detailed eligibility criteria or baseline characteristics, limiting assessment of how closely the analyzed participants represent a broader presbyopia population. It also does not give the randomization sequence-generation or allocation-concealment procedures. The design is recorded as randomized and double-masked, but the practical details of masking and whether it remained successful are not reported.

The primary endpoint is a threshold-based responder outcome at a specified assessment time. It does not report the distribution of visual-acuity changes or the magnitude of change among responders and nonresponders. The registry also does not report longer-term results beyond the posted assessment times, so the duration of any response cannot be determined from these registry entries.

Several statistical details are unavailable: the original sample-size justification, the sponsor regression covariates, model diagnostics, multiplicity procedures, missing-data handling, and sensitivity analyses. The record does not describe interim analyses. The discrepancy flag between the sponsor analysis and the unadjusted recalculation further underscores that the aggregate counts do not reproduce the sponsor's model-based estimate; the sponsor's own analysis takes precedence, but the reason for the difference cannot be established from the record.

Safety summaries are counts and do not provide full event-level descriptions or establish causality. The efficacy analysis population and safety at-risk denominators also differ. These limitations do not negate the posted findings, but they constrain how fully the trial can be independently assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An Evaluation of the Efficacy and Safety of CSF-1 in the Temporary Correction of Presbyopia (NEAR-2) — NCT04599972.
• Registry record last updated 2024-04-04; status last verified 2023-11.
• Results first posted 2023-11-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT04599972, NEAR-2, is a completed Phase 3 randomized, double-masked, vehicle-controlled parallel-group study of CSF-1 for temporary correction of presbyopia. The registry lists enrollment of 304 and a four-visit multi-center design. Both groups used one drop in both eyes twice daily for approximately 2 weeks.

The primary endpoint counted participants meeting the combined visual-acuity responder definition on Day 8, one hour after the first dose. The posted counts were 64 among 154 in the CSF-1 group and 32 among 150 in the vehicle group. The sponsor reported a logistic regression odds ratio of 2.979, with a 95% confidence interval from 1.753 to 5.064 and p < 0.01. The registry flags a discrepancy with the unadjusted recalculation, so the sponsor's analysis takes precedence.

Three secondary responder outcomes show a consistent direction in the reported comparisons. The registry does not report multiplicity handling, missing-data procedures, or several details needed to reproduce the sponsor's model. Safety records include 0 serious adverse events in the CSF-1 group and 1 in the vehicle group, with no deaths reported.