Efficacy and Safety of Ozenoxacin 1% Cream Versus Placebo in the Treatment of Patients With Impetigo: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Ozenoxacin 1% Cream Versus Placebo in the Treatment of Patients With Impetigo (NCT01397461), a randomized phase 3 study. The primary outcome is Clinical Success.

2. Clinical Question

3. Trial Design

This was a Phase III, randomized, parallel-group study described as multicenter. Its title identifies three arms and a comparison of ozenoxacin 1% cream applied twice daily for 5 days with placebo. The registry also lists retapamulin 1% ointment and ozenoxacin placebo as study interventions. The brief summary describes placebo-controlled comparisons of ozenoxacin cream and retapamulin ointment.

The registry classifies the study as triple-masked. Its more detailed summary distinguishes the masking arrangements: the ozenoxacin versus placebo comparison was double-blind, while the investigator was blinded for the retapamulin versus placebo comparison. These descriptions are retained as recorded; further operational details about masking are not reported in the registry record.

Enrollment is recorded as 465. The study started in 2012-03, primary completion was in 2012-12, and the status is completed. The posted primary outcome is clinical success, expressed as a percentage of participants, at the end of therapy (Visit 3), with a timeframe recorded as 2 weeks. The endpoint description identifies the ITTC population.

The registry lists 155 participants in the ozenoxacin 1% cream arm, 156 in the ozenoxacin placebo arm, and 154 in the retapamulin 1% ointment arm for the outcome. The analyses presented compare each active-treatment arm with placebo. Information about allocation concealment, stratification, site-level analysis, adherence, and the trial's original design assumptions is not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

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: The baseline analysis population was considered the safety populations. The safety population was defined as all patients who had at least one application of study drug. One patient was randomised to retapamulin but treated with ozenoxacin. One patient was randomised to retapamulin but not treated.

6. Primary Endpoint

The registry lists the primary outcome as Clinical Success, measured over 2 weeks.

The primary endpoint is clinical success, measured as the percentage of participants with a clinical response at the end of therapy, identified as Visit 3. The timeframe is recorded as 2 weeks. The result is based on whether a participant met a prespecified clinical definition rather than on an average symptom score.

The definition uses the SIRS severity index, which covers seven signs or symptoms: exudate or pus, crusting, erythema or inflammation, tissue warmth, tissue oedema, itching, and pain. Each item is rated on a scale from 0 to 6: zero means absent, scores 1 and 2 indicate mild symptoms, 3 and 4 indicate moderate symptoms, and 5 and 6 indicate severe symptoms. Success required a score of 0 for exudates or pus, crusting, tissue warmth, and pain, and no more than 1 for erythema or inflammation, tissue oedema, and itching. The definition further required that no additional antimicrobial therapy in the affected baseline area be necessary.

A binary endpoint of this kind is useful when the clinical question is whether participants reach a defined response state. It gives a direct proportion for each arm, while the threshold makes clear that success depends on the full set of criteria. It does not show how far participants who did not meet the threshold were from success, or how individual symptoms changed.

7. Results Posted in the Registry

• Ozenoxacin 1% Cream: 34.8% (54/155) versus 19.2% (30/156) on control; risk difference 15.6 percentage points (95% CI 5.9 to 25.3), risk ratio 1.81 (1.23–2.67); unadjusted two-proportion z-test p = 0.002.
• Retapamulin 1% Ointment: 37.7% (58/154) versus 19.2% (30/156) on control; risk difference 18.4 percentage points (95% CI 8.6 to 28.3), risk ratio 1.96 (1.34–2.86); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is classified as meeting or not meeting the registry's clinical-success definition. The arm-level percentages describe the share classified as successful. In general, a binary endpoint is often analyzed by comparing proportions across groups. This gives an interpretable summary, although it compresses the underlying clinical information into a success-versus-not-success classification.

What does the risk difference describe?

The risk difference is the success proportion in one arm minus the success proportion in the comparison arm. In the posted recalculation, the ozenoxacin cream versus placebo estimate is 0.156; the retapamulin ointment versus placebo estimate is 0.184. Because both estimates are positive, the observed success proportion was higher in each active-treatment arm than in placebo. The risk difference uses the absolute difference in proportions, rather than expressing the comparison as a relative multiplier.

Risk differences are often useful for clinical interpretation because they retain the scale of the outcome probability. They are sensitive to the outcome rates in the groups being compared, and their interpretation depends on the endpoint definition and population. The estimate alone does not convey its uncertainty, so it is read alongside the confidence interval and the analysis method.

How should the relative measures be read?

The registry also posts relative measures for the recalculated comparisons. For ozenoxacin cream versus placebo, the risk ratio is 1.812, with limits 1.23 and 2.668, and the odds ratio is 2.246, with limits 1.338 and 3.767. For retapamulin ointment versus placebo, the risk ratio is 1.958, with limits 1.339 and 2.865, and the odds ratio is 2.538, with limits 1.517 and 4.245. In general, a risk ratio compares probabilities, while an odds ratio compares odds; these are not interchangeable quantities. The posted relative measures are additional summaries and do not replace the absolute risk-difference estimates.

What does a confidence interval add?

A confidence interval describes uncertainty around an estimated quantity under the statistical procedure used. In general, a wider interval indicates less precision, while a narrower interval indicates more precision. The 95% confidence intervals for both recalculated risk differences lie above zero. This is consistent with positive risk differences under those calculations. A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it account for sources of uncertainty that were not represented in the calculation, such as limitations in reporting or study conduct.

What do the p-values test?

The recalculated p-values are 0.002 for ozenoxacin cream versus placebo and <0.001 for retapamulin ointment versus placebo. The registry reports p = 0.003 for the sponsor's chi-squared analysis of ozenoxacin cream versus placebo. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming the analysis conditions hold. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry does not report the full statistical plan or the hypotheses and adjustment procedures governing all comparisons.

The recalculations are unadjusted comparisons based on the posted summary counts. They should be distinguished from the sponsor's reported analysis and from any adjusted or population-specific analyses that are not reported in the registry record. The registry identifies the ITTC population for the primary endpoint, but details such as the handling of missing observations, the exact analysis population rules, and any covariate adjustment are not reported.

Why can chi-squared and recalculated results differ?

The sponsor's reported ozenoxacin comparison used a chi-squared test. A chi-squared test evaluates whether the observed distribution across categories differs between groups under the test's assumptions. The recalculated p-value comes from a separate unadjusted calculation based on the posted counts and does not necessarily reproduce every detail of the sponsor's test. Choices about test implementation and analysis population can affect a p-value. Since the registry does not report all those details, the numerical difference between p = 0.003 and the recalculated p-value of 0.002 should not be used to infer a specific methodological choice.

In general, count-based tests rely on sufficient information in the outcome categories and on a suitable comparison structure. The posted counts make the binary outcome and arm denominators explicit. The registry does not report whether additional checks, adjustments, or sensitivity analyses were performed.

These methods quantify evidence and precision for the recorded endpoint. They do not show that the endpoint fully captures every relevant clinical outcome, and they do not answer questions about unreported follow-up or populations beyond the ITTC description.

10. Confidence Intervals and Precision

The confidence intervals quantify sampling uncertainty for the recalculated risk differences. For ozenoxacin 1% cream versus placebo, the estimated risk difference is 0.156, with a 95% confidence interval from 0.059 to 0.253. For retapamulin 1% ointment versus placebo, the estimate is 0.184, with a 95% confidence interval from 0.086 to 0.283. Both intervals are above zero, so the posted recalculations are consistent with a positive difference in clinical success proportions.

The interval endpoints also show that the estimates are not exact measurements of an underlying effect. For each comparison, a range of values remains compatible with the data and the calculation procedure. The range for the retapamulin comparison extends from 0.086 to 0.283, and the range for the ozenoxacin comparison extends from 0.059 to 0.253. The intervals overlap, but overlap alone does not test whether the active-treatment arms differ from each other; the posted comparisons are against placebo.

Precision depends on the amount and distribution of outcome information, as well as the calculation method. The registry posts counts and arm sizes for this endpoint, but further details about missing observations and any sensitivity analysis are not reported in the registry record. The stated confidence intervals therefore should be read as precision estimates for the recalculated comparisons, not as a complete accounting of every possible source of uncertainty.

In general, a confidence interval is not a prediction interval for individual outcomes and does not establish clinical importance. The clinical meaning of any difference depends on the endpoint definition and context, which are not resolved by statistical precision alone.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect in each comparison, with alternative assumptions that the effect to detect is 100%, 75%, or 50% of that observed effect. For ozenoxacin cream versus placebo, planning for 100% of the observed effect gives 126 participants per arm for 80% power and 169 participants per arm for 90% power. Planning for 75% gives 215 participants per arm for 80% power and 287 for 90% power. Planning for 50% gives 458 participants per arm for 80% power and 612 for 90% power.

For retapamulin ointment versus placebo, planning for 100% of the observed effect gives 93 participants per arm for 80% power and 124 for 90% power. Planning for 75% gives 158 participants per arm for 80% power and 211 for 90% power. Planning for 50% gives 335 participants per arm for 80% power and 448 for 90% power.

In plain language, the 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the stated effect under the listed assumptions. The 90% power column uses a higher target chance of detection. For both comparisons, assuming a smaller effect requires more participants per arm. These are planning illustrations, not observed power. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The trial's own original sample-size assumptions are not reported in the registry record.

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 = 0.192; treatment proportion p₁ = 0.348; average p̄ = 0.270.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6281 = 1.2311.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6183 = 0.5204.
4. n = (1.2311 + 0.5204)² / (0.1561)² = 125.9, rounded up to 126 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 <- 0.192307692307692                          # control proportion
p1 <- 0.348387096774194                          # 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(1397461)
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 = 126 (80% power), 169 (90% power)
 75% of observed effect: n per arm = 215 (80% power), 287 (90% power)
 50% of observed effect: n per arm = 458 (80% power), 612 (90% power)
power.prop.test: 125.9 
Simulated power at n = 126 per arm: 0.809 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports the sponsor's chi-squared analysis for ozenoxacin 1% cream versus placebo, with p = 0.003. The recalculated unadjusted analysis for the same comparison gives a risk difference of 0.156, a 95% confidence interval from 0.059 to 0.253, and p = 0.002. Both analyses concern the comparison of ozenoxacin cream with placebo, but they are not identical statistical outputs: one is the sponsor's reported test and the other is a simple unadjusted recalculation from the posted counts.

The small difference between the p-values does not, on its own, establish a meaningful disagreement in the overall interpretation. The registry does not report enough methodological detail to reconstruct the sponsor's analysis fully or identify why its result differs from the recalculation. The sponsor's result should be presented as the trial's own reported analysis; the recalculated estimate adds an unadjusted effect-size description and confidence interval.

The registry's reported chi-squared analysis covers ozenoxacin cream versus placebo. It does not list a sponsor-reported inferential result for retapamulin ointment versus placebo in the posted analysis record. The recalculated result for that comparison should therefore not be described as the sponsor's reported analysis.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clinical success, and the registry lists one outcome measure and one reported analysis. The trial has three arms, with comparisons of ozenoxacin cream versus placebo and retapamulin ointment versus placebo represented in the posted results. The registry does not report whether the investigators planned a multiplicity adjustment across comparisons, specified a testing hierarchy, or treated one comparison as confirmatory and the other as secondary. Without those details, the recalculated p-values are best read as unadjusted results for their individual comparisons, not as evidence that a family-wise error procedure was used.

The primary endpoint description identifies the ITTC population, but the record does not report detailed analysis-population rules. It is therefore unclear from the registry record how participants were classified if outcome data were unavailable, if they did not complete treatment, or if they had deviations from the assigned regimen. The registry does not report the extent of missing primary-outcome data, a method for handling missing data, or sensitivity analyses assessing alternative assumptions. No inference about completeness or the treatment of missing observations can be made from the posted arm-level figures alone.

The record also does not report whether the sponsor's analysis adjusted for baseline characteristics, study center, or other variables. It does not describe interim analyses, a stopping rule, or the original statistical analysis plan. Those details matter when interpreting which analyses were planned in advance and how multiple opportunities for testing were handled, but they are not available in the registry record.

These reporting gaps do not change the values posted for the endpoint, but they limit the ability to assess how the analyses were selected and whether the reported population and methods match an original prespecified plan. The posted recalculations should accordingly be treated as unadjusted summaries, with no claim that they reproduce unreported analytical decisions.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

The registry lists serious adverse events in 0 participants in the ozenoxacin 1% cream group, with 156 at risk; in 0 participants in the ozenoxacin placebo group, with 156 at risk; and in 0 participants in the retapamulin 1% ointment group, with 152 at risk. It also lists other adverse events in 0 participants in each of those groups, with the same respective numbers at risk. No serious adverse-event terms are listed.

These figures describe the adverse-event entries posted in the registry record. Zero reported events does not establish that no adverse events of any kind occurred, nor does it show that uncommon events were ruled out. The registry lists deaths as not reported in the registry record. Further detail about event definitions, follow-up duration for safety, severity, relatedness, withdrawals, or collection procedures is not reported in the registry record.

The at-risk counts shown for safety should not be assumed to match the outcome-analysis denominators: the registry lists 156 at risk for the ozenoxacin cream safety results, while the primary-outcome arm size is 155. Safety results should be read as the registry records them, separately from the clinical-success analysis. They do not provide a complete basis for comparing safety profiles or for making an individual treatment decision.

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

The posted primary-outcome percentages show that clinical success was recorded for 34.8% of participants receiving ozenoxacin 1% cream and 19.2% receiving ozenoxacin placebo. The recalculated risk difference is 0.156, with a 95% confidence interval from 0.059 to 0.253. For retapamulin 1% ointment, the posted percentage is 37.7%, and its recalculated risk difference versus placebo is 0.184, with a 95% confidence interval from 0.086 to 0.283. These are results for the registry-defined endpoint and the ITTC population.

The outcome definition is clinically structured: it combines scores across seven signs and symptoms and requires that additional antimicrobial therapy in the affected baseline area not be necessary. The percentage therefore describes the proportion meeting the full definition, not the average change in symptoms or the proportion improving by any amount. The results do not reveal the distribution of scores among participants who did not meet the success threshold.

The posted comparisons are each against placebo. They do not establish whether ozenoxacin cream and retapamulin ointment differ from one another; no direct active-arm comparison is reported. The endpoint is recorded at Visit 3, with a timeframe of 2 weeks. It does not answer how long the response lasts or what happens at follow-up beyond that assessment.

Statistical evidence and clinical importance are related but distinct. Confidence intervals describe uncertainty around the recalculated risk differences, while p-values describe compatibility with a statistical null model under specific assumptions. Neither alone determines whether a difference is important to patients or applies to people outside the trial. The registry record does not report the complete analytical plan, missing-data handling, or detailed safety follow-up, which constrains interpretation beyond the reported endpoint and comparisons.

17. Why This Trial Matters Statistically

This trial illustrates why a binary clinical endpoint needs a clear definition. “Clinical success” is not a generic label for improvement: it depends on a set of SIRS sign and symptom thresholds and a criterion about whether additional antimicrobial therapy is necessary. A reader can interpret the arm percentages more responsibly by understanding exactly what participants had to meet to count as successful.

It also illustrates the value of reporting both absolute and relative summaries. The recalculated risk differences describe the absolute separation in success proportions, while the risk ratios and odds ratios provide relative comparisons. These measures answer different questions and can give different impressions of scale. Presenting them alongside the arm percentages and counts helps keep the relative summaries anchored to the observed outcome rates.

The comparison structure matters as well. A three-arm trial with two placebo comparisons does not automatically provide a direct test between its active-treatment arms. The registry reports each active arm against placebo, and the posted results should be interpreted within that structure. The record's lack of detail about multiplicity procedures also highlights why the testing plan is important when a study contains multiple comparisons.

Finally, the sponsor's chi-squared result and the unadjusted recalculation are not identical outputs. Showing the reported analysis alongside a simple recalculation makes clear both what the registry says and what can be described from the posted counts, without implying that the recalculation reproduces every feature of the original analysis. This distinction is central to transparent statistical interpretation.

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 registry record gives limited detail about how participants were selected and diagnosed, beyond describing patients with a clinical diagnosis of non-bullous or bullous impetigo. Age eligibility, baseline severity requirements, and other inclusion or exclusion criteria are not reported in the registry record. Generalizability beyond the trial population therefore cannot be assessed from these details alone.

The outcome is reported at Visit 3 and has a timeframe of 2 weeks. Later clinical outcomes and the duration of response are not reported in the registry record. Because clinical success is a threshold-based endpoint, the posted percentages also do not show the range of symptom scores or the amount of change among participants who were not classified as successful.

The registry reports a sponsor chi-squared p-value for ozenoxacin cream versus placebo, but does not give the full statistical analysis plan or enough information to reproduce every aspect of that analysis. Multiplicity handling, missing-data methods, analysis-population rules beyond the ITTC label, and any sensitivity analyses are not reported in the registry record. The retapamulin comparison has recalculated estimates, but a sponsor-reported inferential analysis for that comparison is not listed.

Safety entries list zero serious and zero other adverse events in the groups, but detailed definitions, follow-up, event severity, relatedness, and deaths are not fully available; deaths are not reported in the registry record. These omissions limit conclusions about the completeness of safety reporting. The registry's triple-masking classification and its description of differing masking arrangements are both recorded, but further practical details are not reported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Ozenoxacin 1% Cream Versus Placebo in the Treatment of Patients With Impetigo — NCT01397461.
• Registry record last updated 2016-07-01; status last verified 2016-06.
• Results first posted 2016-05-18.
• 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

NCT01397461 is a completed Phase III randomized, parallel, multicenter study of ozenoxacin 1% cream, ozenoxacin placebo, and retapamulin 1% ointment in patients with a clinical diagnosis of impetigo. Enrollment is recorded as 465. The study started in 2012-03, with primary completion in 2012-12.

The primary outcome was clinical success at Visit 3, within a timeframe recorded as 2 weeks, in the ITTC population. Posted success percentages were 34.8% for ozenoxacin cream, 19.2% for ozenoxacin placebo, and 37.7% for retapamulin ointment. The registry reports a chi-squared p-value of 0.003 for ozenoxacin cream versus placebo; unadjusted recalculations provide risk differences and confidence intervals for both placebo comparisons.

The registry records zero serious and zero other adverse events in the listed groups. Details on missing data, multiplicity, the complete statistical plan, and deaths are not reported in the registry record.