Clinical Trial to Evaluate the Safety and Tolerability of Lagricel® Ofteno Multi-dose Ophthalmic Solution: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial to Evaluate the Safety and Tolerability of Lagricel® Ofteno Multi-dose Ophthalmic Solution (NCT04081610), a randomized phase 1 study. The primary outcome is Presence of Adverse Events (AEs).

2. Clinical Question

The study asks whether the safety and tolerability profile of Lagricel® Ofteno Multidose differs from that of Lagricel® Ofteno Single Dose on the ocular surface of clinically healthy subjects. The registry identifies dry eye as the therapeutic indication, but the stated study objective concerns healthy subjects rather than people being treated for dry eye.

The registry states a null hypothesis of similar safety and tolerability profiles and an alternative hypothesis of different profiles. This is a question about comparative safety and tolerability, not a direct test of benefit for dry eye. The primary outcome is recorded as a participant count, with adverse events classified as present or absent. The record also lists visual acuity, epithelial defects assessed with fluorescein stain and green lissamine, conjunctival hyperemia, and chemosis among the secondary outcomes.

The posted results compare the two arms, but the brief summary and arm-level results describe different evaluable group counts. The summary says 17 evaluable subjects per group, whereas the outcome results list 16 in the multidose arm and 18 in the single-dose arm. The reason for this difference is not reported in the registry record.

3. Trial Design

The registry classifies this as a Phase I, randomized, parallel-group trial with no masking. The brief description calls it single-center, controlled, open, and randomized. Parallel-group means participants were assigned to a study arm rather than both formulations being compared within the same participant over a crossover sequence. The record does not provide further details about the allocation procedure or the conduct of randomization.

The two arms received Lagricel® Ofteno Multidose or Lagricel® Ofteno Single Dose. Both are described as 0.4% hyaluronate ophthalmic solutions from Laboratorios Sophia. The study objective concerns safety and tolerability on the ocular surface in clinically healthy subjects. The registry lists dry eye as the therapeutic indication and lubricant use as the intended context.

The enrollment field reports 34, and the brief summary states that 34 subjects were evaluable, with 17 evaluable subjects per group. However, the posted primary-outcome arm results list 16 participants for the multidose formulation and 18 for the single-dose formulation. The record does not explain this difference, so those descriptions should not be silently treated as interchangeable. The reason for any discrepancy between the summary and outcome counts is not reported in the registry record.

The trial is marked completed. The recorded study start is 2019-09-09 and the primary completion date is 2019-10-23. The stated primary-outcome timeframe is during the 10 days of evaluation, including a safety call on day 11. The brief summary gives an estimated study duration of 5 months; this is distinct from the primary-outcome observation timeframe. Details of dosing frequency, administration instructions, adherence assessment, and the visit schedule are not reported in the registry record.

The record identifies five secondary outcomes: visual acuity, epithelial defects assessed with fluorescein stain, epithelial defects assessed with green lissamine, conjunctival hyperemia, and chemosis. It lists seven outcome measures and 16 analyses overall, but does not explain how those entries map to the listed secondary outcomes.

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 Presence of Adverse Events (AEs), measured over during the 10 days of evaluation, including the safety call (day 11)..

The primary endpoint is the presence of adverse events, recorded for participants. The registry describes the measure as nominal and assessed on a Present / Absent scale, with absent designated as the normal value. The stated timeframe covers the 10 days of evaluation and includes the safety call on day 11.

A binary endpoint reduces each participant’s assessment to whether an adverse event was recorded or not. Reporting the count of participants with an event gives a direct description of how many participants in each arm were affected according to the posted results. The comparison can then be expressed as an absolute difference between the proportions affected, or as a relative measure such as a risk ratio or odds ratio. These measures answer different questions: an absolute difference describes the contrast in event frequency, while relative measures compare the event frequency between arms on a multiplicative scale.

For a safety and tolerability study, collecting adverse-event information is relevant because it records unwanted events during exposure and follow-up. The record does not provide event-level descriptions for the participants counted as having other adverse events, so their nature, timing, severity, and relationship to treatment are not reported in the registry record. It also does not report a more detailed definition of an adverse event or how events were elicited and adjudicated.

The primary endpoint is not itself a measure of clinical benefit for dry eye. It describes event occurrence during the specified evaluation period. Its interpretation depends on the observation window, the completeness of event ascertainment, and how participants with incomplete assessments were handled; those analysis details are not reported in the registry record.

7. Results Posted in the Registry

• Lagricel® Ofteno Single Dose: 44.4% (8/18) versus 43.8% (7/16) on control; risk difference 0.7 percentage points (95% CI -32.7 to 34.1), risk ratio 1.02 (0.48–2.17); unadjusted two-proportion z-test p = 0.968.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry presents a binary primary outcome: participants are classified according to whether an adverse event was present or absent. For this kind of outcome, the event count and the number assessed in each arm describe the observed data. The risk difference expresses the contrast in event proportions as an absolute difference. A value near zero indicates that the observed proportions are close, but the estimate must be read with its confidence interval because it is based on a limited set of observations.

What does the confidence interval describe?

A confidence interval communicates uncertainty around an estimated contrast under the assumptions of the method used. In repeated applications of a compatible procedure, intervals constructed in this way would cover the underlying quantity at the stated confidence level at the specified rate. It is not a range of individual participant outcomes, and it does not assign a probability to the true effect after the data have been observed. Here, the recalculated risk-difference interval extends from -0.327 to 0.341. Because it includes zero and values on either side, the posted estimate does not precisely distinguish the direction or size of the difference. The confidence level and specific interval-construction method for this recalculation are not reported in the registry record.

How should the p-value be read?

The unadjusted p-value for the recalculated risk-difference comparison is 0.968. In general, a p-value describes how unusual the observed data, or more extreme data, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the probability that the observed difference occurred by chance in a simple everyday sense. A large p-value is not proof of no difference. In particular, a conventional difference test is not an equivalence test: equivalence requires a prespecified acceptable range and an analysis that assesses whether the uncertainty is contained within that range. Such an equivalence margin is not reported in the registry record.

Why report both absolute and relative contrasts?

The registry includes a risk difference, risk ratio, and odds ratio. The risk difference describes an absolute contrast in event frequency. The risk ratio compares the event frequencies as a ratio, while the odds ratio compares the odds of an event. Relative measures can be useful for comparing across contexts, but they are not interchangeable with an absolute difference and can be harder to interpret when event frequencies are not rare. All three estimates should be considered alongside their uncertainty intervals and the observed arm counts, rather than taken as stand-alone proof of a safety conclusion.

What does the sponsor analysis test?

The registry reports a Wilcoxon (Mann-Whitney) analysis for median difference in final values, with a reported value of 0.05 and p = 0.409, classified as non-inferiority. The Wilcoxon rank-sum approach compares ranks of observations between groups and does not require the outcome to follow a normal distribution. Although the result is presented using the phrase median difference, the test itself is based on the ordering of observations; its interpretation depends on the outcome and assumptions about the distributions. The record does not identify the specific outcome represented by the final values, give an interval for the estimate, or state the non-inferiority margin. Therefore, the reported p-value alone is insufficient to evaluate the non-inferiority claim.

Why can over-dispersion matter?

For count outcomes, a model that assumes a particular relationship between the average count and its variability can understate uncertainty when the observed variability is greater than that assumption permits. This is called over-dispersion. It can make standard errors too small and confidence intervals too narrow if it is not addressed. The primary endpoint in this record is a participant-level binary outcome rather than a count of repeated events, and the registry does not report an over-dispersion model. This general issue would be relevant if repeated event counts or other count outcomes were analyzed, but the analysis details for the listed secondary outcomes are not reported in the registry record.

The registry identifies the trial as randomized, open, and parallel-group. Random allocation can help balance measured and unmeasured characteristics on average, but it does not ensure balance in a small trial. Open conduct means masking was absent, so participant and study-team knowledge of assigned formulation could potentially influence reporting or assessment. The record does not describe procedures intended to reduce that possibility. The posted primary-outcome recalculation is unadjusted; any covariate-adjusted analysis or other analysis of the primary endpoint is not reported in the registry record.

Finally, the study summary says 17 evaluable subjects per group, while the primary outcome results list 16 and 18. Statistical interpretation depends on knowing which participants were included and how missing or unevaluable assessments were treated. The registry does not reconcile the counts or report a missing-data method or analysis population definition. These omissions limit how fully the posted comparisons can be assessed.

10. Confidence Intervals and Precision

The primary-outcome risk difference is 0.007, with a confidence interval from -0.327 to 0.341. The interval is wide relative to the point estimate and includes zero, as well as possible differences favoring either arm. This indicates substantial uncertainty about the size and direction of the contrast. The point estimate should not be mistaken for a precise estimate simply because it is close to zero.

The relative estimates also have broad intervals: the risk ratio is 1.016, with an interval from 0.476 to 2.169, and the odds ratio is 1.029, with an interval from 0.265 to 3.993. Each interval includes the value representing no relative contrast. Their breadth means the data do not tightly constrain the possible relative differences. The intervals should not be interpreted as establishing equivalence or excluding clinically important differences, especially because the registry does not report an acceptable equivalence or non-inferiority margin.

Confidence intervals reflect sampling uncertainty under the analysis method; they do not account automatically for every limitation in measurement, conduct, or reporting. The record does not state the confidence level or interval method for the recalculated estimates. It also does not report how missing outcome values were handled, and the outcome counts do not match the evaluable group counts in the brief summary. Those reporting gaps add uncertainty about the exact analysis population and prevent a full assessment of precision.

Overall, the estimates are compatible with a range of possible contrasts. The absence of a statistically small p-value is not a substitute for precision, and the near-zero point estimate is not by itself evidence of similar safety profiles.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the original trial design calculation. For this binary outcome, the entries are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and the statistical model are correct. The 90% power column gives the corresponding planning figure for a design with a 90% chance under the same assumptions. These are planning probabilities for hypothetical future designs, not probabilities that the observed result is correct.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The figures rise as the fraction of the observed effect becomes smaller. This is the usual planning pattern: smaller effects are harder to distinguish from random variation and need more participants for the same target power, all else held constant. The posted values should be treated cautiously because the observed effect itself is uncertain, as reflected in its broad interval.

This is not observed power. It does not measure how much power the completed trial actually had after its results were known, nor does it establish that the study could detect or exclude a particular clinically meaningful difference. The sample-size curve should be read as an illustration of the relationship between the assumed effect size and the planning requirement under the stated assumptions, not as a reconstruction of the trial’s original design.

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 = 0.438; treatment proportion p₁ = 0.444; average p̄ = 0.441.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7022 = 1.3762.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7021 = 0.5909.
4. n = (1.3762 + 0.5909)² / (0.0069)² = 80,241.8, rounded up to 80,242 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 <- 0.4375                          # control proportion
p1 <- 0.444444444444444                          # 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(4081610)
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 = 80,242 (80% power), 107,421 (90% power)
 75% of observed effect: n per arm = 142,594 (80% power), 190,892 (90% power)
 50% of observed effect: n per arm = 320,701 (80% power), 429,326 (90% power)
power.prop.test: 80241.8 
Simulated power at n = 80,242 per arm: 0.800 (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 a sponsor analysis using Wilcoxon (Mann-Whitney), with median difference in final values of 0.05, p = 0.409, and a non-inferiority classification. This is distinct from the unadjusted recalculation for the posted binary primary outcome, which reports a risk difference of 0.007, an interval from -0.327 to 0.341, and p = 0.968. The estimates should not be treated as two versions of the same test: the registry describes different analysis methods and different outcome summaries.

The sponsor analysis does not include a confidence interval in the record, and the non-inferiority margin is not reported. Those details are needed to judge what range of differences the analysis was designed to rule out and whether its criterion was satisfied. The record also does not clearly identify which final-value measure is represented by the sponsor analysis. The p-value and classification alone therefore do not establish a non-inferiority conclusion.

The registry does not flag a discrepancy between the posted sponsor result and the recalculation. The recalculation is a simple, unadjusted comparison based on the posted primary-outcome summary statistics; it does not replace or reproduce the sponsor’s distinct analysis. Neither result should be interpreted as proof of equivalence. The reported analyses address the posted data and do not resolve missing details about outcome definitions, analysis populations, or incomplete assessments.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome of adverse events and five secondary outcomes: visual acuity, epithelial defects assessed with fluorescein stain, epithelial defects assessed with green lissamine, conjunctival hyperemia, and chemosis. It also reports seven outcome measures and 16 analyses. The record does not explain how the listed outcomes and analyses relate to one another, which analyses were prespecified, or which were considered confirmatory.

When many outcomes or comparisons are examined, the chance of at least one apparently notable result can increase. Statistical methods can address this multiplicity in different ways, but the registry record does not report whether any adjustment was used, whether outcomes were ranked in a testing hierarchy, or how the analyses were interpreted across the full set. The recalculated primary-outcome p-value is explicitly unadjusted. No adjustment should be presumed for the other analyses.

Information about missing data and analysis populations is also limited. The brief summary describes 17 evaluable subjects per group, while the primary-outcome arm results give 16 and 18. The reason for these different counts is not reported in the registry record. There is no reported explanation of exclusions, withdrawals, incomplete outcome assessments, or whether participants were analyzed according to randomized assignment. The record does not state how missing values were handled or whether a sensitivity analysis was performed.

These omissions matter because the analysis population and missing-data approach can affect both the estimated event proportions and their uncertainty. Without a clear account of who contributed data to each outcome, it is difficult to assess whether the posted analysis represents all randomized participants, only those with evaluable data, or another population. The record also does not report a statistical analysis plan, so the timing and prespecification of the reported comparisons cannot be assessed.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse-event summary reports zero serious adverse events among 16 participants at risk in the Lagricel® Ofteno Multidose arm and zero among 18 at risk in the Lagricel® Ofteno Single Dose arm. Deaths are reported as zero in each arm. The registry lists no top serious-event terms. These are the posted serious-event counts; they do not establish that serious events are impossible or that the formulations have identical serious-event risks.

The serious-event figures should be kept separate from the primary endpoint and from the counts of other adverse events. The primary outcome reports 7 participants with other adverse events in the multidose arm and 8 in the single-dose arm. Thus, the record reports other adverse events even though it reports no serious adverse events. The specific non-serious events, their severity, timing, and relationship to the study formulations are not reported in the registry record.

The summary covers a short evaluation timeframe described as during the 10 days of evaluation, including the safety call on day 11. These figures describe what was reported during that period; they are not a complete characterization of safety outside the recorded observation window. The registry does not report additional follow-up or detailed methods for collecting and classifying adverse events.

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

The posted primary-outcome results show adverse events recorded for 7 participants in the multidose arm and 8 participants in the single-dose arm. The unadjusted recalculated risk difference is 0.007, but its interval extends from -0.327 to 0.341. The estimate is therefore uncertain and does not tightly determine either the direction or magnitude of a difference. The associated p-value of 0.968 does not establish that the formulations have the same safety and tolerability profile.

The registry’s separate Wilcoxon (Mann-Whitney) result is labelled non-inferiority, with a reported median difference of 0.05 and p = 0.409. The record does not provide the non-inferiority margin, an interval for that estimate, or a clear description of the final-value outcome analyzed. The posted result therefore cannot, by itself, show whether a defined non-inferiority criterion was met.

The serious-event summary reports no serious adverse events and no deaths in either arm during the recorded evaluation. That finding is limited to the reported study population and period. It does not erase the other adverse events recorded in both groups, nor does it describe their clinical features or establish how they were related to treatment.

This study addresses short-term safety and tolerability in clinically healthy subjects. It does not directly establish effectiveness for dry eye, and the findings should not be generalized beyond the population, formulations, and observation period described without further evidence. The registry record does not report enough information to determine how the observed data compare with a clinically acceptable safety difference. In particular, no equivalence or non-inferiority margin is reported, and the difference between the evaluable group counts in the summary and outcome results is unexplained.

The appropriate statistical reading is that the record gives a small set of observed event counts and uncertain comparative estimates. It does not demonstrate that either formulation is safer, that the safety profiles are equivalent, or that a clinically important difference has been ruled out.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of the distinction between a small observed difference and a precise conclusion. The posted event counts are close in absolute terms, and the recalculated point estimate is near zero. Yet the confidence interval spans differences in either direction. A reader should therefore focus not only on the point estimate or p-value, but also on how much uncertainty remains around the contrast.

The record also illustrates why a non-significant result is not the same as evidence of equivalence. A claim that two products have sufficiently similar outcomes generally requires a prespecified margin defining how much difference would be acceptable and an analysis designed to assess that margin. The registry labels a separate analysis as non-inferiority, but the margin and other essential details are not reported. The label alone cannot settle the statistical question.

Safety reporting requires attention to outcome definitions. The serious-event summary reports no serious events, while the primary outcome reports other adverse events in both groups. These are not contradictory results: they describe different levels or categories of events. The absence of reported serious events should not be confused with an absence of all adverse events.

Finally, the record shows why clear accounting of participants matters. The summary’s evaluable group counts differ from those attached to the posted primary outcome, and the reason is not explained. Without details on analysis populations, missing data, and the relation between the outcomes and analyses, readers cannot fully assess how the results were produced or how broadly they apply.

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 leaves several trial-specific uncertainties. The brief summary states 17 evaluable subjects per group, but the primary-outcome results list 16 in the multidose arm and 18 in the single-dose arm. The reason for the difference is not reported in the registry record. This makes it difficult to understand which participants contributed to the posted primary comparison and whether any outcome data were unavailable.

The record does not report the original statistical analysis plan, the sample-size justification, or the rationale for the enrollment target. The planning illustration based on the observed effect is not a substitute for those original design details. It also does not report a non-inferiority margin, even though the sponsor analysis is classified as non-inferiority. A confidence interval for that sponsor analysis is absent, and the specific final-value measure is not clearly identified.

The primary outcome is described as present or absent, but event-level details for the other adverse events are not reported. The record does not provide their nature, severity, timing, duration, or relationship to the formulations. It gives no detailed description of event ascertainment or adjudication. The serious-event summary reports zero events in each arm, but the short evaluation window limits the timeframe represented by that summary.

The trial is described as open and unmasked. The registry does not report procedures to reduce the potential influence of treatment knowledge on reporting or assessment. Details of allocation concealment, dosing, adherence, and follow-up beyond the stated evaluation period are not reported in the registry record.

Lastly, the registry lists multiple outcome measures and analyses but does not describe multiplicity control or identify which analyses were prespecified. These limitations do not invalidate the posted counts, but they constrain how confidently the estimates can be interpreted and generalized.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Trial to Evaluate the Safety and Tolerability of Lagricel® Ofteno Multi-dose Ophthalmic Solution — NCT04081610.
• Registry record last updated 2021-05-03; status last verified 2021-03.
• Results first posted 2021-05-03.
• 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

NCT04081610 is a completed, randomized, open, parallel-group Phase I study comparing Lagricel® Ofteno Multidose with Lagricel® Ofteno Single Dose in clinically healthy subjects. Both formulations are described as 0.4% hyaluronate ophthalmic solutions. The primary outcome is the presence or absence of adverse events during the 10 days of evaluation, including the safety call on day 11.

The primary results list 7 participants with adverse events among 16 in the multidose arm and 8 among 18 in the single-dose arm. The unadjusted recalculated risk difference is 0.007, with an interval from -0.327 to 0.341 and p = 0.968. The registry separately reports a Wilcoxon (Mann-Whitney) analysis labelled non-inferiority, but the margin and other details needed to assess that claim are not reported.

The record reports no serious adverse events and no deaths in either arm. It does not reconcile the outcome counts with the brief summary’s evaluable group counts or report detailed missing-data and multiplicity methods. The results describe the posted observations and do not establish equivalence or effectiveness for dry eye.