Moxifloxacin AF Ophthalmic Solution for Treatment of Bacterial Conjunctivitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Moxifloxacin AF Ophthalmic Solution for Treatment of Bacterial Conjunctivitis (NCT00759148), a randomized phase 3 study. The primary outcome is Clinical Cure at the Day 4 (EOT)/Exit Visit.

2. Clinical Question

The trial asked whether clinical and microbiological outcomes at the Day 4 exit visit differed between moxifloxacin AF ophthalmic solution and its vehicle in patients with bacterial conjunctivitis. The registry describes the intended population as patients one month of age or older. Its primary outcome was clinical cure, defined using the study eye; microbiological success was a secondary outcome.

The question is about the difference in observed proportions under the two randomized treatment assignments, not about outcomes in every person with conjunctivitis. The registry reports the primary population definition and the outcome timing, but details such as how missing Day 4 assessments were handled are not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group study. It compared Moxifloxacin AF with the Moxifloxacin AF vehicle, using the same stated dosing schedule in both arms: one drop in each eye twice daily for 3 days. The registry identifies bacterial conjunctivitis as the condition under study and describes the intended age range as one month or older.

The registry reports an enrollment of 1179. For the primary endpoint, the posted analysis includes 424 participants in the Moxifloxacin AF arm and 423 in the vehicle arm. These endpoint denominators belong to the specified Microbiological Intent-to-Treat Analysis Set, not necessarily to every person enrolled. The safety figures use separate at-risk denominators, so they should not be treated as the same analysis population.

The study started in 2008-10, had primary completion in 2010-03, and is recorded as completed. Alcon Research is listed as sponsor. Randomization helps balance factors that can affect outcomes across treatment groups on average; masking is intended to limit influences on care, assessment, and reporting. The registry identifies quadruple masking but does not describe which roles were masked or how masking was maintained.

The record does not report the trial's original sample-size assumptions, allocation ratio, specific randomization procedure, or detailed statistical analysis plan. Planning illustrations based on the observed results are not evidence of what assumptions were used when the trial was designed. The registry also records no reported analyses, so the posted comparisons should be read as descriptive or recalculated summaries rather than as a complete account of a sponsor's prespecified analysis.

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.

Before assignment: 1179 subjects with bacterial conjunctivitis were randomized and treated to Moxifloxacin AF or Moxifloxacin AF vehicle.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: This analysis population includes all patients who received drug, had at least 1 on-therapy visit and were pathogen positive for bacteria on Day 1 (Microbiological Intent-to-Treat (MBITT) Analysis Set).

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.

Population: This population analysis includes all subjects who received study drug (Safety Analysis Set).

6. Primary Endpoint

The registry lists the primary outcome as Clinical Cure at the Day 4 (EOT)/Exit Visit, measured over Day 4.

The primary endpoint was clinical cure at the Day 4 end-of-treatment or exit visit. Cure required the sum of two cardinal ocular signs of bacterial conjunctivitis—bulbar conjunctival injection and conjunctival discharge or exudate—to be zero, meaning both signs were normal or absent. Assessment took place 12–48 hours after the last dose. The outcome is expressed as the percentage of participants meeting that definition, and only one eye, designated the study eye, contributed to the analysis.

A binary endpoint such as cure/not cure turns each participant's assessment into a category. The reported percentage therefore describes how common the defined outcome was in the analyzed group; it does not measure the degree of change in each sign or the time course of improvement. A standardized definition supports comparison between randomized arms, while the Day 4 timing makes the endpoint an assessment at a particular visit rather than a measure of longer-term status.

The primary population was restricted to participants who received drug, had at least one on-therapy visit, and were pathogen positive for bacteria on Day 1. This population definition is important to interpretation: the endpoint percentage describes those meeting the analysis-set criteria. How participants without an assessable Day 4 outcome were treated in the calculation is not reported in the registry record.

7. Results Posted in the Registry

• Moxifloxacin AF: 62.5% (265/424) versus 50.6% (214/423) on control; risk difference 11.9 percentage points (95% CI 5.3 to 18.5), risk ratio 1.24 (1.10–1.39); 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.

Microbiological Success at the Day 4 (EOT)/Exit Visit

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Moxifloxacin AF: 74.5% (316/424) versus 56.0% (237/423) on control; risk difference 18.5 percentage points (95% CI 12.2 to 24.8), risk ratio 1.33 (1.20–1.47); 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 Moxifloxacin AF than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary endpoint concerns microbiological success at the same Day 4 exit visit. Its overall direction is consistent with the primary clinical-cure result: the observed proportion favored the Moxifloxacin AF arm over vehicle. This provides a related but not identical view of outcome, because microbiological success concerns pathogen status whereas clinical cure is defined by ocular signs.

Agreement in direction across endpoints can add context, but the outcomes are not independent confirmations simply because they are listed separately. They were assessed in the same trial and at the same visit, and may reflect overlapping features of the disease process. The clinical endpoint remains the designated primary outcome; the secondary result should be interpreted as supporting context rather than as a replacement for the primary question.

The registry posts an unadjusted comparison for the secondary endpoint, but does not report an adjustment for examining multiple outcomes. In general, evaluating multiple endpoints creates more opportunities for an apparently notable result to arise by chance. Adjusting for multiplicity can change the interpretation of individual p-values, while prioritizing a prespecified primary endpoint can help keep the main inference focused. The record does not state a multiplicity strategy, so the secondary p-value should not be treated as if it had been adjusted or as definitive evidence on its own.

The registry lists one secondary outcome and no reported analyses. It does not describe whether additional outcomes were considered in the original protocol, how the endpoint hierarchy was set, or whether results were selected for posting according to a prespecified plan. The secondary endpoint's relationship to the primary result is therefore best understood descriptively: it points in the same observed direction, but its weight is limited by its secondary status, unadjusted inference, and the lack of a reported analysis plan.

Secondary outcomes can be useful for checking whether distinct measurements tell a broadly coherent story. They can also differ from the primary outcome because their measurement properties and biological meanings differ. A reader should retain those distinctions and avoid collapsing clinical and microbiological outcomes into a single claim.

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

• Microbiological Success at the Day 4 (EOT)/Exit Visit

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant in the analysis population either met the clinical-cure definition at the scheduled assessment or did not. The reported percentage is the number meeting the definition relative to the endpoint denominator, expressed as a percentage. For the primary endpoint, the posted denominators are 424 for Moxifloxacin AF and 423 for vehicle. Because the registry defines a restricted analysis population, these denominators should be interpreted in that context rather than as the enrollment count.

What does a risk difference express?

A risk difference is the contrast between two outcome proportions on an additive scale. It describes the gap between the proportion in one group and the proportion in the comparator group. Positive values, under the comparison's stated direction, indicate a larger proportion in the named treatment arm. The registry reports a risk-difference estimate and an interval for the primary comparison. The posted percentages also make the direction of the observed contrast visible without requiring a model-based interpretation.

Risk differences are often easier to relate to absolute frequencies than ratio measures, but their size depends on the baseline proportion in the comparator group. A given relative contrast can correspond to different absolute differences when baseline risks differ. Conversely, the same absolute difference can represent a different relative contrast in settings with different baseline proportions. The two scales answer related but distinct questions and should not be treated as interchangeable.

What do the relative measures add?

The relative risk compares the outcome proportion in one group with the proportion in the other. The posted primary relative-risk estimate is 1.235, with an interval from 1.096 to 1.392. An estimate above 1 indicates that the outcome proportion is higher in the named arm for the comparison as oriented. The odds ratio is another relative measure, but it compares odds rather than probabilities. Odds and probabilities are not identical, so an odds ratio should not be described as if it were a risk ratio, particularly when the outcome is not rare.

These are alternative descriptions of the same binary-outcome comparison, not separate independent findings. Reporting more than one scale can help readers understand the contrast, but it does not provide multiple replications of the result. The registry does not identify a more complex adjusted model for these estimates. The available comparison is unadjusted and should be read as such.

How should the p-value be understood?

The posted primary p-value is p < 0.001 and is labeled unadjusted. In general, a p-value assesses how unusual data at least as discrepant as those observed would be under a specified null model, if the model's assumptions hold. It does not tell a reader the probability that the treatment groups are truly equal, and it is not a measure of the magnitude of the group contrast. A small p-value can accompany an effect whose practical importance requires separate judgment; a larger p-value can arise when information is limited even if an estimate is not exactly zero.

Random assignment supports comparison of the groups, but interpretation still depends on the analysis population, outcome definition, missing-data handling, and the validity of the statistical calculation. The registry does not report the statistical test, confidence-interval method, or adjustment variables. Those details should not be inferred from the existence of an estimate or p-value.

Why do intervals matter?

An interval estimate conveys uncertainty around an estimated contrast. In general, it gives a range of values compatible with the data and the method used, rather than a guarantee that the true effect lies within that range. Its width reflects both the amount of information and the variability relevant to the calculation. An interval is more informative than a point estimate alone because it shows how much precision the data support. The registry's comparison includes interval estimates, but the confidence level and interval-construction method are not reported in the registry record.

For a ratio measure, the value representing no relative difference is 1; for a difference measure, it is 0. Whether an interval includes the relevant null value is one way to assess compatibility with no difference under the interval method. This is a general statistical interpretation, not a substitute for considering the estimate's size, endpoint, population, and limitations. The relative-risk interval for the primary comparison is reported from 1.096 to 1.392, so it does not include 1. No inference about other populations or outcomes follows automatically.

What does recalculation mean?

A recalculated comparison is an unadjusted calculation based on the posted summary counts and proportions. It does not recover participant-level data, account for variables that may have been used in a sponsor model, or establish the method chosen in the original analysis plan. Here the record marks no discrepancy between its posted result and the recalculation, but the registry also lists no reported analyses. Consequently, the recalculated summary should not be mistaken for a complete report of the trial's statistical analysis. Any adjustment, subgroup evaluation, or sensitivity analysis not described in the record is not reported in the registry record.

In general, randomized parallel-group trials are analyzed by comparing outcome distributions across assigned groups. The simplicity of a binary endpoint allows direct reporting of proportions and absolute or relative contrasts. Nonetheless, valid inference requires careful handling of participants who do not have an observed outcome, adherence to the stated population, and transparent reporting of the methods used. The registry provides the endpoint definition and analysis-set criteria, but not enough detail to reconstruct all those decisions.

11. Confidence Intervals and Precision

The posted primary percentages are 62.5% for Moxifloxacin AF and 50.6% for vehicle. The registry also reports an interval for the risk-difference comparison, though its bounds are not repeated in this explanation. The relative-risk estimate is 1.235, with an interval from 1.096 to 1.392. That interval describes uncertainty on the ratio scale, not on the absolute percentage scale.

In general, an interval estimate helps distinguish a precise estimate from one that remains compatible with a wider range of effects. Narrower intervals indicate greater precision under the method used; broader intervals indicate more uncertainty. An interval is not a promise that the true effect lies within its limits, and it does not account for sources of uncertainty omitted from the analysis, such as unreported missing-data assumptions or model choices.

The relative-risk interval does not include 1, the null value for a ratio comparing equal outcome proportions. This is consistent with the reported unadjusted p-value of p < 0.001, while neither statistic answers whether the effect is important for every clinical or research context. The registry does not report the confidence level or method used to construct its intervals. The interval should therefore be read as the estimate's reported uncertainty range, without attributing an unreported procedure to it.

Precision also depends on what is being estimated. The endpoint concerns one clinical assessment at Day 4 in a defined analysis set, with one eye contributing per participant. It does not directly quantify uncertainty about later outcomes, other populations, or outcomes defined in a different way. The reported precision belongs to the specific contrast and endpoint, not to every interpretation of the trial.

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, not total events. They are illustrations derived from the observed effect, rather than the trial's original design calculations. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios use the full observed effect and smaller fractions of it. The trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm for the same assumed effect. These are planning targets, not guarantees: actual power depends on the true effect, variability, analysis method, and other features of a study.

Smaller effects are harder to distinguish from random variation, so the illustration requires more participants per arm when it assumes a smaller fraction of the observed effect. The displayed scenarios are useful for understanding how planning needs change as the target effect changes, but the observed effect can be unstable and may not be a suitable design target for another trial. The figures are not observed power and do not describe the probability that this completed trial detected its true effect.

The record does not report the assumptions used to choose the trial's enrollment or its original planned power. These planning illustrations cannot be used to infer those missing design choices, nor do they demonstrate that the trial was planned around the effect seen in the posted results.

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 = 0.506; treatment proportion p₁ = 0.625; average p̄ = 0.565.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7010 = 1.3740.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6959 = 0.5857.
4. n = (1.3740 + 0.5857)² / (0.1191)² = 270.8, rounded up to 271 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 <- 0.505910165484634                          # control proportion
p1 <- 0.625                          # 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(759148)
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 = 271 (80% power), 363 (90% power)
 75% of observed effect: n per arm = 486 (80% power), 650 (90% power)
 50% of observed effect: n per arm = 1,101 (80% power), 1,473 (90% power)
power.prop.test: 270.8 
Simulated power at n = 271 per arm: 0.807 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies clinical cure as the primary outcome and microbiological success as a secondary outcome. It reports an unadjusted p-value for each posted comparison, but the statistical plan and multiplicity procedure are not reported in the registry record. It is therefore unknown whether the original analysis controlled the chance of false-positive findings across outcomes, whether a formal hierarchy was specified, or whether additional comparisons were planned.

Multiplicity matters when several hypotheses are tested. In general, the more opportunities there are to declare a result notable, the more cautious interpretation of individual unadjusted p-values may be warranted. This does not invalidate the posted results, but it means a secondary p-value should be understood as unadjusted unless an adjustment is documented. The registry record does not provide enough information to determine the intended family of tests or any correction method.

The primary analysis population is defined as participants who received drug, had at least one on-therapy visit, and were pathogen positive for bacteria on Day 1. This definition clarifies who contributed to the primary endpoint analysis. It is not a full account of the handling of all randomized participants. The registry does not report reasons for exclusion from this set, a separate intention-to-treat analysis, or results in other populations.

Missing endpoint data can affect both the estimated proportion and its uncertainty. In general, possible approaches include analyzing observed cases under stated assumptions, imputing unobserved outcomes, or conducting sensitivity analyses. The registry does not report how missing Day 4 assessments were handled, the amount of missing outcome data, or whether sensitivity analyses were conducted. No particular missing-data procedure should be assumed.

The record lists zero reported analyses. That absence limits what can be established about prespecification, covariate adjustment, subgroup work, or robustness checks. It does not establish that no such work occurred; those details are simply not reported in the registry record. The posted summary is thus interpretable at the level of the stated endpoint and population, while important aspects of the analysis process remain undocumented.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The registry reports zero serious adverse events among 593 participants at risk in the Moxifloxacin AF group and zero among 586 at risk in the vehicle group. It also reports zero other adverse events in each of those at-risk groups and zero deaths in each group. These are the registry's posted counts, not a statement that no adverse events of any kind occurred in every participant.

The safety denominators differ from the primary endpoint denominators because the registry reports them for separate safety groups. They should not be combined with the clinical-cure analysis population or treated as interchangeable. The record does not provide event-term details for non-serious adverse events, and no serious-event terms are listed. It also does not describe duration of safety follow-up or the method used to collect events.

Zero reported events in a study does not establish that an event is impossible or that risk is absent. In general, event counts are interpreted in relation to the population observed, the observation period, and the completeness of reporting. The posted figures describe the registry record and do not support conclusions about safety beyond those limits.

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

The posted results show a higher observed clinical-cure percentage in the Moxifloxacin AF arm than in the vehicle arm at the Day 4 exit visit, within the specified primary analysis population. The unadjusted comparison is reported as p < 0.001, and the relative-risk estimate and its interval indicate the direction and uncertainty of that particular comparison. The secondary microbiological endpoint has a concordant observed direction, while the registry's safety figures report no serious adverse events, other adverse events, or deaths in the listed groups.

These findings do not establish what would happen in every patient, in populations outside the stated analysis set, or at times beyond the Day 4 assessment. The primary endpoint used one study eye and a specific threshold-based definition of cure. It does not capture every symptom, each participant's degree of change, or longer-term outcomes. The results also do not establish that the clinical and microbiological measures are interchangeable.

A low unadjusted p-value does not measure the probability that a treatment effect is real, nor does it determine whether an observed contrast is important in practice. Statistical evidence, effect magnitude, measurement validity, patient context, and safety monitoring are distinct considerations. The registry does not report a full sponsor analysis, the original statistical plan, or enough detail to evaluate all assumptions behind the posted comparisons.

Likewise, zero reported adverse-event counts should not be interpreted as proof of no risk. Their meaning depends on the safety population, observation period, and reporting. The record's limited safety detail does not establish how events were collected or what follow-up occurred.

The appropriate statistical reading is therefore specific: the observed Day 4 outcome proportions differed in the posted comparison, with uncertainty described by the registry's interval estimates, in the defined endpoint population. Broader claims about other outcomes, longer-term effects, all eligible patients, or unreported analyses are not established by these summaries.

17. Why This Trial Matters Statistically

This trial illustrates why an endpoint definition and analysis population matter as much as an overall enrollment figure. The primary result is not simply a percentage among everyone enrolled: it is a percentage in a defined Microbiological Intent-to-Treat Analysis Set, using one study eye and a specific clinical-cure rule. Readers who overlook those conditions may attribute the estimate to a broader population than the posted analysis represents.

It also illustrates the value of reporting effects on more than one scale. A risk difference describes an absolute contrast, while relative risk and odds ratio describe relative contrasts. Each scale answers a different interpretive question, and none should be substituted for another without explanation. Interval estimates add information about precision, whereas a p-value alone does not describe effect size or uncertainty fully.

The secondary microbiological result offers a related perspective, but outcome multiplicity affects how much inferential weight to place on it. Without a reported multiplicity plan, the primary endpoint and unadjusted secondary result should not be treated as equivalent evidence. The record's lack of a detailed analysis report also makes transparent distinctions between posted descriptive results and a prespecified sponsor analysis especially important.

Finally, the planning illustrations show a general design principle: aiming to detect a smaller effect requires more participants per arm under the stated assumptions. They are not a reconstruction of the original design. Keeping that distinction clear prevents a post hoc illustration from being mistaken for a trial's original sample-size justification or for observed power.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary assessment is limited to Day 4, 12–48 hours after the last dose. It describes outcome at that visit rather than persistence or later recurrence. The treatment schedule lasted 3 days, but the registry does not provide longer-term outcome results in the posted material.

The clinical-cure measure is a binary threshold based on two ocular signs, and only one eye contributed to the primary analysis. This focuses the comparison on a defined clinical state, but it does not retain detail about changes in each sign or the other eye. The primary population is restricted to participants who received drug, had at least one on-therapy visit, and were pathogen positive on Day 1; results for other analysis populations are not reported.

Important analysis details are unavailable in the registry record. The statistical test and interval method, confidence level, handling of missing Day 4 assessments, and any sensitivity analyses are not reported. The record lists zero reported analyses and does not state whether multiplicity was addressed. Consequently, the posted unadjusted comparisons cannot be evaluated against a complete prespecified analysis plan.

The safety summary gives at-risk denominators and event counts, but not the duration or method of safety surveillance, detailed non-serious event terms, or additional event-level context. Zero posted counts should be read within those reporting limits.

Finally, the planning illustrations use fractions of the observed effect and stated generic assumptions. The original enrollment rationale and design assumptions are not reported. Those illustrations cannot establish the trial's intended detectable effect or substitute for the unavailable original design documentation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Moxifloxacin AF Ophthalmic Solution for Treatment of Bacterial Conjunctivitis — NCT00759148.
• Registry record last updated 2018-01-02; status last verified 2017-12.
• Results first posted 2011-03-22.
• 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

NCT00759148 is a completed, randomized, quadruple-masked, parallel-group Phase 3 study sponsored by Alcon Research. It evaluated Moxifloxacin AF ophthalmic solution 0.5% against Moxifloxacin AF vehicle in bacterial conjunctivitis, with one drop in each eye twice daily for 3 days in both arms. The intended population included patients one month of age or older.

The primary outcome was clinical cure at the Day 4 exit visit, assessed in a defined microbiological intent-to-treat population using one study eye. The posted clinical-cure proportions were 62.5% for Moxifloxacin AF and 50.6% for vehicle, with an unadjusted comparison of p < 0.001. Microbiological success was listed as a secondary outcome. The registry also posts safety counts and planning illustrations based on observed effects.

The study started in 2008-10 and reached primary completion in 2010-03. The record does not report the original sample-size assumptions, detailed statistical plan, missing-data methods, or multiplicity strategy. These omissions limit interpretation beyond the outcomes and populations described in the posted results.