Efficacy and Safety of Chloroprocaine 3% Gel and Oxybuprocaine 0.4% Eye Drops Anesthesia in Pediatric Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Chloroprocaine 3% Gel and Oxybuprocaine 0.4% Eye Drops Anesthesia in Pediatric Population (NCT05926258), a randomized phase 3 study. The primary outcome is Conjunctiva Anesthesia With Chloroprocaine 3% Eye Gel as Compared With Oxybuprocaine Chlorhydrate 0.4% Eye Drops.

2. Clinical Question

The clinical question is whether the two assigned anesthetic products differ in the probability of successful conjunctival anesthesia in children undergoing an ocular examination that requires surface anesthesia. The primary outcome records whether anesthesia was successful in the right eye, assessed with an eye spear sponge five minutes after the study product was administered.

The question concerns a short-term, defined examination outcome under the trial’s administration and assessment procedures. It is not a comparison of all possible uses, settings, or durations of either product. The registry record does not report a broader endpoint definition, details of the examination procedures, or further eligibility criteria.

3. Trial Design

The registry identifies this as a Phase 3, randomized, parallel-group clinical trial with single masking. Participants were assigned to chloroprocaine 3% gel or oxybuprocaine 0.4% solution. The planned enrollment is 74, and the brief summary describes 1:1 randomization. The record does not identify who was masked, so the meaning of single masking for participants, clinicians, or outcome assessors is not specified in the registry record. The trial is listed as completed.

Both products were administered in both eyes by the investigator or a deputy at the clinical centre on study day 1. Each administration consisted of two drops given one at a time at a one-minute interval. The primary outcome concerns the right eye only and was assessed five minutes after study product administration, immediately before ocular examination, using an eye spear sponge. Although treatment was administered to both eyes, the posted primary endpoint is not a combined measure of both eyes.

The endpoint results list 19 participants with successful anesthesia among 37 in the chloroprocaine group and 23 among 36 in the oxybuprocaine group. These are the denominators attached to the posted outcome, not an explanation of the number completing each trial activity. The reason the endpoint denominators differ from the listed enrollment is not reported in the registry record.

The registry lists adverse events and global tolerance graded as secondary outcomes. It does not report secondary outcome results in the posted results. The original sample-size justification, allocation concealment procedures, detailed analysis populations, missing-data procedures, and any interim analyses are not reported in the registry record. The record also does not give a fuller account of the protocol beyond the design and administration details stated above.

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 Conjunctiva Anesthesia With Chloroprocaine 3% Eye Gel as Compared With Oxybuprocaine Chlorhydrate 0.4% Eye Drops, measured over day 1.

The primary endpoint counts participants with successful conjunctival anesthesia in the right eye. Success was assessed five minutes after study product administration and immediately before the ocular examination, using an eye spear sponge. It is a binary participant-level outcome: each participant is counted as having or not having the defined successful anesthesia outcome. The registry does not give further criteria for classifying the sponge assessment as successful.

This endpoint is used to make a direct comparison between assigned groups on a specific, near-term clinical task. In general, a binary endpoint can be expressed as the number of participants with the event and the number assessed in each group, or as the proportion with the event. Here the event is successful anesthesia, not an adverse event. The posted counts are 19 of 37 for chloroprocaine and 23 of 36 for oxybuprocaine.

The endpoint’s specified timing and eye matter to interpretation. The outcome addresses the right eye at the five-minute assessment, even though the assigned product was instilled in both eyes. It does not by itself summarize anesthesia in both eyes, performance at other time points, or other aspects of ocular examination. The registry record does not report a separate endpoint for the left eye or describe how any bilateral observations were handled in the analysis.

As a measure, the endpoint gives a clinically interpretable count of participants meeting the trial’s success criterion, but its precision depends on the number assessed and the number of successes. The posted comparison includes a confidence interval that allows a range of group differences compatible with the data and analysis. The endpoint’s clinical meaning also depends on the success criterion and assessment process, details of which are only partly described in the registry record.

7. Results Posted in the Registry

• Oxybuprocaine 0,4% Solution: 63.9% (23/36) versus 51.4% (19/37) on control; risk difference 12.5 percentage points (95% CI -9.9 to 35.0), risk ratio 1.24 (0.84–1.85); unadjusted two-proportion z-test p = 0.279.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: a participant either met the registry’s definition of successful right-eye conjunctival anesthesia at the specified assessment or did not. The posted group counts are 19 successes among 37 participants for chloroprocaine and 23 among 36 for oxybuprocaine. The comparison is reported as a risk difference, with additional risk-ratio and odds-ratio measures. Each measure expresses the contrast between groups on a different scale.

What does the risk difference express?

The risk difference subtracts one group’s event probability from the other group’s event probability. In this comparison, the estimate is defined for oxybuprocaine relative to chloroprocaine and is 0.125. A positive estimate indicates a higher observed event proportion in the oxybuprocaine group. The difference is an absolute contrast, rather than a relative multiplier. Its 95% confidence interval is -0.100 to 0.350, which includes no difference and values in either direction. The interval is important because the point estimate alone does not convey how uncertain the comparison is.

What do the relative measures add?

The risk ratio compares the probabilities of success between groups as a ratio. Its estimate is 1.244, with a confidence interval from 0.835 to 1.853. The odds ratio compares the odds of success rather than the probabilities; its estimate is 1.676, with a confidence interval from 0.657 to 4.278. For either relative measure, a value of one represents no relative difference. Each interval includes that value, consistent with substantial uncertainty in the relative comparison. Odds ratios can appear farther from one than risk ratios when outcomes are not rare, so a relative measure should be read on its own scale and alongside the event counts and risk difference.

How should the p-value be read?

The unadjusted p-value is 0.279. In general, a p-value describes the degree of compatibility between data and a specified null model, assuming that model and the test’s conditions. It is not a measure of effect size, and it does not state the probability that a finding is due to chance or that the treatments are the same. The registry record does not specify an adjusted analysis or a multiplicity procedure for the primary comparison. The posted p-value is therefore described as unadjusted, without assuming details of the trial’s full statistical plan.

What does randomization contribute?

In general, random assignment aims to make treatment groups comparable at the start with respect to both measured and unmeasured characteristics, apart from variation that can arise by chance. That rationale supports interpreting a group contrast as an estimate of the effect of assignment under the trial conditions. Randomization does not ensure equal group characteristics in a particular trial, and it does not protect against every source of bias after assignment. The registry record identifies randomized parallel-group allocation but does not report the sequence-generation method or allocation concealment process.

Masking can reduce the influence of expectations on care or outcome assessment, depending on who is masked and how outcomes are measured. The registry lists single masking, but who was masked is not reported in the registry record. The outcome was assessed with an eye spear sponge, but further information about assessor training, reproducibility, or the criteria for a successful assessment is not reported.

All posted calculations should be understood in relation to the defined participant-level endpoint. Treatment was instilled in both eyes, but the primary outcome was recorded for the right eye. The registry record does not describe a bilateral analysis or a model for eye-level data. Since the reported endpoint is participant-level and tied to one specified eye, the posted comparison does not require treating two eyes from one participant as separate independent observations.

The analysis population and handling of unavailable outcome assessments are not reported in the registry record. In general, an analysis based on randomized assignment and an analysis limited to participants with observed endpoint data can answer different questions when outcomes are missing or treatment is not received as assigned. The registry entry does not explain which approach was used, whether any participants were excluded from the endpoint analysis, or how missing values were treated. Accordingly, the posted denominators should be read as the denominators for the recorded endpoint comparison, without inferring a particular analysis population.

Confidence intervals and p-values address sampling uncertainty under their statistical assumptions. They do not account automatically for limitations in trial conduct, outcome definition, missing data, or generalizability. The registry record does not provide the full statistical analysis plan, the original sample-size justification, or details of interim monitoring. No assumption about those unreported procedures should be added to the interpretation.

10. Confidence Intervals and Precision

The 95% confidence interval for the risk difference, expressed as oxybuprocaine compared with chloroprocaine, is -0.100 to 0.350 around an estimate of 0.125. This range conveys appreciable uncertainty about the size and direction of the group contrast. It includes no difference and also includes differences favoring either group. The estimate is therefore not precise enough to rule out a range of possible effects on the absolute probability of successful anesthesia.

In general, a confidence interval is a range produced by a statistical procedure that, under its assumptions and repeated use, would contain the underlying parameter at the stated rate. It is not a statement that there is a 95% probability that this particular fixed parameter lies inside this particular interval. Nor does the interval represent every kind of uncertainty: it does not automatically incorporate bias, outcome misclassification, missing-data concerns, or limitations in the trial’s conduct.

The relative measures also have broad intervals. The risk ratio is 1.244, with a 95% confidence interval from 0.835 to 1.853; the odds ratio is 1.676, with a 95% confidence interval from 0.657 to 4.278. Those ranges include the no-relative-difference value of one. Their width reflects that the posted counts do not determine the relative comparison with high precision.

Precision should be considered alongside the number of outcome observations, the outcome definition, and the design. The registry lists enrollment of 74, while the endpoint comparison reports denominators of 37 and 36. The reason for the difference is not reported in the registry record. Without further information on the analysis population and missing assessments, the confidence intervals describe uncertainty for the posted comparison but cannot resolve whether any unreported data issues affect interpretation.

A wide interval is not proof that there is no effect; it indicates that the data are compatible with a range of effects. Likewise, a point estimate alone should not be treated as a stable or definitive estimate. Whether any value in the interval would be clinically meaningful cannot be judged from the registry record, which does not report a threshold for a clinically important difference.

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 participants and not total events. They are illustrations calculated from the observed effect under stated planning assumptions, rather than a record of the trial’s original design justification. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each planning scenario, the effect to detect is the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation would require to have an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions were correct. The 90% power column gives the corresponding number per arm for a 90% chance. Power is a property of a planned design for a particular assumed effect and analysis; it does not describe the probability that the observed result is true.

Planning for 100% of the observed effect gives 243 participants per arm for 80% power and 325 participants per arm for 90% power. Planning for 75% of the observed effect gives 437 participants per arm for 80% power and 584 participants per arm for 90% power. Planning for 50% of the observed effect gives 990 participants per arm for 80% power and 1,325 participants per arm for 90% power. The pattern illustrates a general planning principle: smaller target effects require more participants to detect them at the same power and significance level.

These are planning illustrations based on the observed effect, not observed power for the completed trial. They are sensitive to the assumptions used and to the observed estimate on which they are based. The original sample-size assumptions and justification for this trial are not reported in the registry record, so the illustrations should not be read as the trial’s planned enrollment target or as evidence that the original design had a particular power.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.514; treatment proportion p₁ = 0.639; average p̄ = 0.576.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6988 = 1.3697.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6932 = 0.5834.
4. n = (1.3697 + 0.5834)² / (0.1254)² = 242.7, rounded up to 243 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 <- 0.513513513513513                          # control proportion
p1 <- 0.638888888888889                          # 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(5926258)
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 = 243 (80% power), 325 (90% power)
 75% of observed effect: n per arm = 437 (80% power), 584 (90% power)
 50% of observed effect: n per arm = 990 (80% power), 1,325 (90% power)
power.prop.test: 242.7 
Simulated power at n = 243 per arm: 0.797 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and two secondary outcomes: number of participants with adverse events and product global tolerance graded. Secondary outcome results are not reported in the registry record. The record does not report a multiplicity adjustment or a hierarchy of hypotheses, so it is not possible to determine how the trial’s original analysis plan addressed the chance of false-positive findings across multiple outcomes. The posted primary p-value is unadjusted and should be read as such.

In general, multiplicity arises when several outcomes, treatment contrasts, subgroups, or analyses are tested. The more questions tested, the greater the chance that at least one result may appear statistically notable by chance if no adjustment or prespecified testing strategy is used. This general issue does not establish that an error occurred in this trial; it explains why knowledge of the prespecified analysis plan matters. That plan is not reported in the registry record.

The registry record does not report how missing primary outcome observations were handled, whether all randomized participants were included in the analysis, or what analysis population was used. The posted primary outcome denominators are 37 for chloroprocaine and 36 for oxybuprocaine, while listed enrollment is 74. The reason for this difference is not reported in the registry record. It is also not reported whether participants had missing assessments, were excluded for other reasons, or were analyzed according to a particular treatment-received or randomized-assignment rule.

In general, missing outcome data can affect a comparison if the likelihood of missingness is related to treatment or outcome. An analysis restricted to observed outcomes and an analysis that accounts for missing outcomes may rely on different assumptions. Without a stated method and information about missingness, no such assumptions can be evaluated from the registry record.

Randomization is identified, but the record does not report sequence generation or allocation concealment. Single masking is listed, but the masked role or roles are not specified. The registry also does not report interim analyses, subgroup analyses, or a complete statistical analysis plan. These omissions limit assessment of prespecification and analytic flexibility; they do not establish that any particular analysis or procedure was or was not carried out.

14. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The posted serious adverse event counts are zero in both groups: zero among 37 participants assigned to chloroprocaine and zero among 36 assigned to oxybuprocaine. Deaths are also recorded as zero in both groups. For other adverse events, the registry lists one affected participant among 37 in the chloroprocaine group and none among 36 in the oxybuprocaine group.

These are counts of participants, not counts of every event episode. Zero recorded serious adverse events means none were reported in the posted results for the listed groups; it does not establish that the risk of a serious event is zero. With limited numbers of participants, uncommon events may not be observed. The registry record does not give details about the nature, timing, severity, or relatedness of the one other adverse event, and the serious-event terms list is empty.

The registry lists global tolerance graded as a secondary outcome, but its results are not reported in the registry record. The safety counts should therefore be interpreted as the limited adverse-event information posted, not as a complete characterization of tolerability or all possible harms. No conclusion about comparative safety can be drawn from these small counts alone.

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

The primary result is a comparison of successful right-eye conjunctival anesthesia at a defined assessment: five minutes after study product administration, before ocular examination, using an eye spear sponge. Success was recorded in 19 of 37 chloroprocaine participants and 23 of 36 oxybuprocaine participants. The risk-difference estimate is positive for oxybuprocaine relative to chloroprocaine, but its 95% confidence interval extends from -0.100 to 0.350 and includes no difference.

The result therefore describes the observed group counts and a range of statistically compatible differences, rather than establishing that one product is superior or that the products are equivalent. The unadjusted p-value of 0.279 does not demonstrate equality. A failure to obtain a small p-value is not a test of equivalence or non-inferiority, and the registry record does not report an equivalence margin, non-inferiority margin, or such a design.

The finding is specific to the enrolled pediatric participants, the administration procedure, the short assessment interval, the right-eye outcome, and the trial’s setting. It does not establish performance for other procedures, other time points, other patient groups, or different administration practices. The record describes ages 0–17 years, but subgroup results by age or other participant characteristics are not reported in the registry record.

The statistical uncertainty is only one part of interpretation. The record lists randomized allocation and single masking, but does not specify who was masked, how allocation was concealed, or which analysis population was used. The reason the endpoint denominators differ from listed enrollment is not reported. The registry does not provide the full statistical plan or secondary outcome results. These gaps mean the posted results cannot answer every question about trial conduct or completeness.

For safety, the posted results include no serious adverse events or deaths in either group, one other adverse event in the chloroprocaine group, and none in the oxybuprocaine group. These counts are too limited to define the full safety profile or rule out uncommon events. The results describe recorded observations; they are not medical advice or a recommendation about product choice.

16. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation of a randomized comparison requires more than comparing the two observed success counts. The primary outcome is straightforward to describe, but the estimated group difference carries uncertainty. Its confidence interval includes no difference and allows effects in either direction, while the unadjusted p-value is 0.279. A point estimate that favors one group in the observed sample should not be mistaken for a precise or definitive estimate of the underlying difference.

The use of multiple effect scales is informative. The risk difference gives an absolute comparison, while the risk ratio and odds ratio express relative contrasts. Their intervals also include their respective no-difference values. Comparing effect estimates and intervals across scales helps distinguish the observed direction from the certainty of the evidence. It also shows why a single p-value cannot convey the size, relevance, or precision of a result.

The design details shape the scope of the conclusion. Participants were randomized in a parallel-group trial, and the endpoint is assessed in the right eye five minutes after administration. Treatment was placed in both eyes, but the reported primary endpoint is not an average of both eyes. The endpoint is therefore anchored to a specific task and time, rather than a general measure of ocular anesthesia over time.

Sample-size illustrations show how assumptions about the target effect and desired power affect planning. Smaller target effects require more participants per arm under the stated planning method. Because these illustrations use the observed effect, they are not substitutes for the trial’s original sample-size justification, which is not reported in the registry record.

Finally, the registry entry highlights the value of transparent reporting. Details about who was masked, analysis populations, missing data, and multiplicity would help readers assess the robustness of the comparison. Their absence limits what can be concluded from the posted record, without changing the reported counts or implying that any particular procedure was omitted in practice.

17. 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 posted primary comparison has limited precision, as reflected by the 95% confidence interval for the risk difference from -0.100 to 0.350. The interval includes no difference and effects in either direction. The registry lists an enrollment of 74, but the endpoint denominators are 37 and 36. Why the posted denominators differ from enrollment is not reported in the registry record, and the analysis population is not specified.

The endpoint definition is tied to success in the right eye five minutes after administration, assessed by eye spear sponge. The registry record does not give further criteria for success, information on assessor training or reproducibility, or results for the left eye. The administered treatment was given to both eyes, so the posted endpoint does not characterize a bilateral outcome.

The record identifies single masking but does not say who was masked. It also does not report the method of sequence generation, allocation concealment, missing-data handling, or whether all randomized participants were included in the primary analysis. These details would help assess potential bias and the relationship between randomization and the reported comparison.

The trial’s original sample-size justification and statistical analysis plan are not reported in the registry record. The planning illustrations based on the observed effect cannot establish what assumptions were used in the original design. The record does not report an adjustment for multiple testing, interim analyses, or subgroup results. Secondary outcomes are listed, but results for global tolerance are not reported in the registry record.

The adverse-event information is limited to posted counts: no serious adverse events or deaths in either group, one other adverse event in the chloroprocaine group, and none in the oxybuprocaine group. Details about event type, severity, timing, and relatedness are not reported. These limitations restrict interpretation to the recorded short-term endpoint and safety counts; they do not establish the presence or absence of unreported trial procedures or outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Efficacy and Safety of Chloroprocaine 3% Gel and Oxybuprocaine 0.4% Eye Drops Anesthesia in Pediatric Population — NCT05926258.
• Registry record last updated 2026-03-09; status last verified 2026-01.
• Results first posted 2026-03-09.
• 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.

21. Record Summary

The registry record describes a completed Phase 3 randomized, parallel-group trial comparing chloroprocaine 3% gel with oxybuprocaine 0.4% solution in pediatric participants aged 0–17 years. Listed enrollment is 74, and the primary endpoint is the number of participants with successful right-eye conjunctival anesthesia five minutes after administration on study day 1.

Successful anesthesia was recorded in 19 of 37 participants in the chloroprocaine group and 23 of 36 in the oxybuprocaine group. The risk difference for oxybuprocaine compared with chloroprocaine is 0.125, with a 95% confidence interval from -0.100 to 0.350; the unadjusted p-value is 0.279. The registry also lists adverse events and global tolerance as secondary outcomes, but global tolerance results are not reported.

Posted safety counts include zero serious adverse events and zero deaths in each group, one other adverse event in the chloroprocaine group, and none in the oxybuprocaine group. Details of the other adverse event, the original sample-size justification, analysis populations, missing-data procedures, and the full statistical plan are not reported in the registry record.