Phase 3 Study of OTO-201 in Acute Otitis Externa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Study of OTO-201 in Acute Otitis Externa (NCT02801370), a randomized phase 3 study. The primary outcome is Number of Subjects Considered a Clinical Cure at Day 8.

2. Clinical Question

3. Trial Design

The registry describes a prospective, randomized, double-blind, sham-controlled, multicenter Phase 3 study. It lists triple masking and random allocation. The study summary says eligible subjects with acute otitis externa were assigned to receive a single administration of 12 mg OTO-201 or sham control, administered to the external auditory canal of the affected ear or ears. The control is described as an empty syringe.

The registry reports enrollment of 262 and lists 130 participants in each arm for the primary outcome. The study status is completed. The recorded study start is 2016-06, and primary completion is recorded as 2016-11. These dates describe the registry record and do not establish when results were analyzed or reported.

The outcome population is called the intent-to-treat analysis set, with an added qualification: it includes randomized subjects who did not have Group A Streptococci cultured on Day 1. The registry record does not explain this qualification, give further details about the randomization procedure, or report the allocation ratio as a formal design detail. The equal arm sizes in the posted primary outcome data and the equal-allocation assumption in the planning illustration are stated separately from any unreported original design specifications.

There is a naming inconsistency in the record. The study summary and randomized arm name identify OTO-201, while the intervention list includes “12 mg ciprofloxacin.” The record does not clarify that label. The endpoint description also names Day 8 in its title and timeframe but refers to clinical signs at Day 15 in its definition. These points limit how confidently the intervention and primary outcome can be described using the registry record alone.

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

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat analysis set: All subjects who were randomized and did not have Group A Streptococci cultured on Day 1

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: 262 subjects randomized (132 sham, 130 OTO-201). 2 sham subjects positive for Group A strep and not in ITT population (Baseline characteristics and efficacy) leaving 130 sham, 130 OTO-201. ITT subjects analyzed as randomized. Safety population (AE/SAE) analyzed by what was received (132 sham, 127 OTO-201) regardless of culture, but had be dosed.

6. Primary Endpoint

The registry lists the primary outcome as Number of Subjects Considered a Clinical Cure at Day 8, measured over At Day 8 (1 week after dosing).

The primary endpoint is titled “Number of Subjects Considered a Clinical Cure at Day 8,” with the timeframe stated as Day 8, one week after dosing. The outcome is a binary count: participants are classified as clinical cures or not. The posted counts are 91 of 130 in the 12 mg OTO-201 arm and 63 of 130 in the control arm.

The registry defines clinical cure by requiring scores of 0 for edema, erythema, otorrhea, and otalgia. Each sign is graded from none to severe, with the levels represented by scores of 0 through 3. A sign score of 0 therefore means none of that sign was recorded under this grading scheme. The registry description, however, says these signs were all scored at Day 15, despite the endpoint’s Day 8 title and timeframe. The record does not reconcile these different assessment days.

A clinical-cure count gives a clinically interpretable summary of the number meeting the stated criteria at an assessment. It reduces several graded signs to a single responder outcome, which makes the arm comparison straightforward to read. That simplification also means the count does not show the full pattern of scores for each sign. No further endpoint rationale or additional scoring detail is reported in the registry record.

7. Results Posted in the Registry

• 12 mg OTO-201: 70.0% (91/130) versus 48.5% (63/130) on control; risk difference 21.5 percentage points (95% CI 9.9 to 33.2), risk ratio 1.44 (1.17–1.78); 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.

Number of Subjects Considered a Clinical Cure at Day 15

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • 12 mg OTO-201: 74.6% (97/130) versus 53.1% (69/130) on control; risk difference 21.5 percentage points (95% CI 10.2 to 32.9), risk ratio 1.41 (1.16–1.70); 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 12 mg OTO-201 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary endpoint: clinical cure at Day 15. Its posted counts follow the same overall direction as the primary comparison, with more participants meeting the cure criterion in the 12 mg OTO-201 arm than in control. The secondary comparison also has an unadjusted p-value of <0.001. This broad consistency supports the observation that the posted results favor the OTO-201-labeled arm on the reported cure counts at both assessment labels.

The secondary endpoint is related to the primary endpoint because both use the clinical-cure concept and the same listed clinical signs. The Day 15 assessment may appear to provide a later outcome alongside the primary endpoint, but the primary definition itself also refers to Day 15 despite its Day 8 title. The record’s timing inconsistency means the relationship between the two endpoint results is not fully clear. The endpoint labels alone do not establish that the primary and secondary results represent distinct assessment times as intended.

Unadjusted secondary results carry less weight when several outcomes or comparisons may be considered. In general, examining multiple outcomes increases the chance that at least one result appears statistically notable by chance, unless the analysis plan accounts for multiplicity. The registry does not report a multiplicity procedure, a hierarchy among outcomes, or a detailed secondary analysis plan. The secondary finding should therefore be viewed as supportive descriptive evidence, not as a separately confirmed conclusion with a documented adjustment for multiple testing.

The registry reports no analyses in its secondary analysis listing. That absence does not erase the posted summary comparison, but it leaves the analysis details unavailable. No further secondary endpoints are listed in the registry record, and no additional secondary interpretation should be inferred from the posted result.

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

• Number of Subjects Considered a Clinical Cure at Day 15

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

In general, a risk difference compares the probability of an outcome between two groups by subtracting one group’s probability from the other’s. A value above zero, when the intervention arm is compared with control in that direction, indicates a larger observed proportion in the intervention arm. The posted primary comparison reports a positive risk difference, and its confidence interval is entirely above zero. The registry record does not report an adjusted risk difference or a covariate-adjusted analysis.

The risk difference is an absolute measure: it expresses the contrast on the outcome-probability scale. It is not interchangeable with a risk ratio or an odds ratio. The posted risk ratio for the primary outcome is 1.444, and the posted odds ratio is 2.481. These are relative measures and can look different in magnitude from an absolute difference, particularly when the outcome is not rare. All three measures describe the same arm comparison from different perspectives; none alone establishes clinical importance.

How should the risk ratio and odds ratio be read?

In general, a risk ratio compares the outcome probability in one group with that in another. A ratio of 1 represents equal probabilities; a ratio above 1 represents a higher probability in the numerator group. For the primary result, the posted risk ratio is 1.444, with interval limits of 1.171 and 1.782. An odds ratio compares odds rather than probabilities. Its posted value is 2.481, with interval limits of 1.492 and 4.128. Because odds and probabilities are different quantities, the odds ratio should not be paraphrased as a probability ratio.

These relative measures depend on which group is treated as the comparison reference. The registry comparison labels the intervention arm and identifies control as the comparison arm. Reading the measures in that direction avoids reversing their interpretation.

What does the p-value add?

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the test assumptions apply. The primary comparison is reported with an unadjusted p-value of <0.001. This is not a measure of effect size, and it does not state the probability that the treatment has no effect. A small p-value also does not remove uncertainty about the magnitude of the effect, which is why the interval estimates matter.

The registry record does not describe the test used, whether it was one-sided or two-sided for the outcome comparison, or the statistical analysis plan. The planning illustration does specify a two-sided significance level of 0.05, but that planning assumption should not be treated as proof of the original outcome-analysis procedure.

What does an interval communicate?

In general, a confidence interval gives a range of values compatible with the data and the method used to construct the interval. A narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the effect size. The primary risk-ratio interval lies above 1, and the risk-difference interval lies above zero. Those features indicate that the posted interval estimates do not include their respective null values. The registry record does not identify the interval construction method or state a confidence level, so neither should be inferred from the posted limits.

How should the binary endpoint be understood?

The primary outcome is a binary classification of clinical cure, reported as a participant count. Binary outcomes are often summarized by the number meeting the criterion and the number assessed in each arm, followed by an absolute or relative comparison. Here the arm counts and denominators are posted. The definition combines four clinical signs into a single all-signs criterion; the result does not separately communicate each sign’s contribution.

The reported analysis population is described as randomized subjects without Group A Streptococci cultured on Day 1. The outcome denominators in the posted arm results are 130 in each arm. The record does not explain how missing outcome assessments were handled or whether any additional exclusions were applied. This matters because a count-based comparison depends on who is included in the denominator and how unavailable outcome information is treated.

What is not documented?

The registry record reports zero analyses in its analysis listing and no reported analyses for the secondary endpoint, while posting summary outcome comparisons. It does not report a full statistical analysis plan, adjustment variables, the chosen test for the primary comparison, interim analyses, a missing-data method, or multiplicity control. These omissions do not change the posted counts, but they limit an independent assessment of how the comparisons were specified and carried out.

The analysis also has an endpoint-definition discrepancy: the title and timeframe refer to Day 8, while the description refers to Day 15. Statistical methods can compare the posted counts, but they cannot resolve which timepoint the counts represent. That clarification is not reported in the registry record.

11. Confidence Intervals and Precision

Precision is conveyed most directly by the interval estimates around the effect measures. For the primary endpoint, the posted risk-ratio estimate is 1.444, with limits from 1.171 to 1.782. This interval excludes 1, the null value for a ratio. The risk-difference interval is also entirely above zero, its null value. These features describe the direction of the estimated contrast across the reported interval; they do not show that every value in the interval is equally plausible or establish the clinical importance of the contrast.

The registry record does not state the confidence level or the method used to calculate the intervals. Therefore, the limits can be reported as posted, but a particular confidence level or calculation procedure cannot be assigned from the registry information alone. In general, an interval is useful because it shows a range of effect sizes compatible with the observed data under the method’s assumptions, rather than reducing the result to a single estimate.

The arm counts are 91 of 130 and 63 of 130 for the primary endpoint. The underlying difference is estimated from those observed counts, but the registry comparison’s risk-difference estimate is reported to four decimal places. Since effect values should not be restated with more than three decimal places, the estimate is best read in the posted results rather than reproduced. Its direction and interval can be described without inventing a rounded value.

Precision is also limited by reporting ambiguity. The outcome title identifies Day 8, while the definition refers to Day 15. The record does not clarify which assessment generated the primary counts, and the interval cannot resolve that issue. The intervention label also differs between the summary and arm name on one hand and the intervention listing on the other. These are reporting limitations, distinct from statistical sampling uncertainty.

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 calculated from the observed effect, not the original trial’s design justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each planning scenario, the effect to detect is a stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm required to have an 80% chance of detecting the specified effect under those assumptions, if the effect and planning model were correct. The 90% power column gives the corresponding requirement for a 90% chance. These are design-planning quantities, not descriptions of the probability that the completed trial’s result is correct. The figures are not observed power.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The required participants per arm increase as the assumed effect becomes smaller. This is a general property of planning: when a study is intended to detect a subtler difference, more information is needed to distinguish it from random variation.

The record does not report the original sample-size justification or original design assumptions. The illustrations should therefore be read as conditional examples based on the posted effect and stated planning assumptions, not as evidence of what the investigators planned before the trial. They also do not account for design features or analysis choices not specified in the registry record.

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 = 0.485; treatment proportion p₁ = 0.700; average p̄ = 0.592.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6950 = 1.3621.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6781 = 0.5707.
4. n = (1.3621 + 0.5707)² / (0.2154)² = 80.5, rounded up to 81 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 <- 0.484615384615385                          # control proportion
p1 <- 0.7                          # 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(2801370)
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 = 81 (80% power), 108 (90% power)
 75% of observed effect: n per arm = 147 (80% power), 196 (90% power)
 50% of observed effect: n per arm = 336 (80% power), 449 (90% power)
power.prop.test: 80.5 
Simulated power at n = 81 per arm: 0.796 (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 record does not report whether multiplicity was addressed. Multiplicity arises when more than one outcome, timepoint, or statistical comparison is examined. In general, making multiple inferential comparisons without an adjustment can increase the chance of a result appearing statistically notable by chance. The record lists a primary clinical-cure endpoint and a secondary clinical-cure endpoint, but it does not document a testing hierarchy, a family of outcomes, or an adjustment procedure. The posted p-values are explicitly unadjusted.

Missing-data handling is also not reported in the registry record. The outcome results provide arm denominators, but the record does not state whether these represent all participants in the defined analysis population at each assessment, how unavailable assessments were treated, or whether any imputation or sensitivity analyses were used. Without that information, readers cannot assess how missing outcome observations might affect the cure counts or the comparison.

The primary population is described as the intent-to-treat analysis set, qualified as randomized subjects who did not have Group A Streptococci cultured on Day 1. The record does not explain the rationale for that qualification, whether any randomized participants were excluded under it, or how it relates to the general use of an intent-to-treat population. It also does not report a separate per-protocol or safety-analysis definition beyond the denominators stated for the adverse-event summaries.

The registry’s analysis listings do not provide a statistical analysis plan, covariate adjustments, interim-analysis details, or the test used for the posted comparisons. These items are not reported in the registry record and should not be inferred from the p-values or planning assumptions. In addition, the Day 8 title and Day 15 endpoint definition leave the primary assessment time unresolved. Together, these reporting gaps limit assessment of prespecification and robustness, while leaving the posted outcome counts intact as descriptive registry results.

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 2% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event summary reports serious adverse events in 0 participants in each arm. For other adverse events, it reports 12 of 127 participants at risk in the 12 mg OTO-201 arm and 18 of 132 in the control arm. The record reports 0 deaths in each arm. These are descriptive counts as recorded; they do not by themselves establish that the arms differ in safety or that an event was caused by the assigned intervention.

The adverse-event denominators differ from the primary endpoint denominators. The registry does not explain the difference or provide further detail about the safety analysis population. It also lists no serious-event terms among the top serious terms. The posted record does not give event-level descriptions, severity breakdowns for the other adverse events, exposure-adjusted rates, or a comparative statistical analysis.

In general, a zero count means no events of that category were recorded in the stated group and analysis period; it does not demonstrate that the underlying risk is zero. The registry record does not report a specific safety follow-up window in the adverse-event summary, so the counts should not be extended beyond the information recorded there.

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

The posted primary comparison shows more participants classified as clinical cures in the 12 mg OTO-201 arm than in control: 91 of 130 compared with 63 of 130. The reported risk ratio is 1.444, with an interval from 1.171 to 1.782, and the unadjusted p-value is <0.001. These results describe the observed trial data and the estimated comparison; they do not, by themselves, establish the clinical importance of the difference or guarantee that the same pattern would occur in other settings.

A statistically notable result is not the same as proof of a treatment effect. The p-value depends on a null model and analysis assumptions, while the interval conveys uncertainty in the estimated comparison. The registry record does not report the full statistical analysis plan or the method used for the comparison. Nor does it state a threshold for a clinically important difference. The posted statistics therefore support a description of the observed contrast but cannot answer every question about its importance or reliability.

The registry also leaves material ambiguities. The endpoint title and timeframe specify Day 8, while its definition refers to signs assessed at Day 15. The intervention is named OTO-201 in the summary and arm results, but the intervention list includes “12 mg ciprofloxacin.” The record does not explain either inconsistency. The observed counts should be interpreted using the posted arm and endpoint labels, with those limitations made explicit.

The secondary cure result follows the same general direction, but its p-value is unadjusted and the record does not describe multiplicity control. The adverse-event summaries report zero serious adverse events in both arms and other adverse events in both arms; those counts are descriptive and do not establish comparative safety. The registry does not report missing-data methods, detailed analysis methods, or further safety context.

Accordingly, the result means that the registry’s posted primary cure counts and comparison favored the OTO-201-labeled arm in this trial. It does not establish a universal or definitive conclusion, resolve the endpoint timing or intervention naming discrepancies, or replace the need to consider the underlying study methods and completeness of reporting.

17. Why This Trial Matters Statistically

This trial is statistically informative because it reports a randomized, sham-controlled comparison and provides arm-level counts for a binary clinical-cure outcome. The posted results include both absolute and relative comparison measures, interval estimates, and an unadjusted p-value. Seeing these quantities together helps distinguish the observed direction of the result from the uncertainty around its size and from the question of statistical compatibility with a null comparison.

The record also illustrates why endpoint definitions and labels matter as much as calculations. A primary endpoint titled for Day 8 is defined using signs assessed at Day 15. That discrepancy cannot be repaired by a more precise estimate or a smaller p-value. It changes the clinical interpretation of what the endpoint timing represents. Similarly, the intervention naming difference between the summary and arm result and the intervention listing affects clarity about what was compared.

The secondary result has a similar direction to the primary comparison, but both are unadjusted and no multiplicity strategy is reported. This is a useful reminder that consistency across related endpoints can be descriptive without constituting independent confirmation. Statistical interpretation depends on the relationship among endpoints and how the analysis plan treated them, information not reported in the registry record.

The planning illustrations also show the distinction between observed trial findings and future study design. Their participant requirements depend on the selected fraction of the observed effect and stated assumptions; smaller target effects require more participants. They are not evidence of the original design rationale or of the completed trial’s power.

Finally, the posted safety counts are useful for transparent description but are not a full comparative safety analysis. Together, these features make the record valuable for understanding how results, uncertainty, design assumptions, and reporting limitations should be considered separately.

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.

Several limitations are specific to the registry record. The primary endpoint is titled and timed for Day 8, but its definition says the clinical signs were assessed at Day 15. The record does not clarify which assessment day generated the primary counts. This prevents a fully secure interpretation of the timing of the primary clinical-cure result.

The intervention names are inconsistent. The study summary and randomized arm identify 12 mg OTO-201, whereas the intervention listing includes “12 mg ciprofloxacin.” The registry does not explain whether this is a labeling error or how the listing relates to the intervention named in the results. Interpretation should use the arm label in the posted comparison without assuming a resolution.

The registry does not report detailed eligibility criteria, the randomization procedure, the original sample-size justification, or the statistical analysis plan. It also does not describe the test used for the primary comparison, covariate adjustment, missing-data handling, multiplicity control, or interim analyses. These omissions constrain assessment of prespecification and robustness.

The reported analysis population is qualified by the absence of Group A Streptococci cultured on Day 1, but the rationale and consequences of that qualification are not described. The registry does not explain the relationship between the primary endpoint denominators and the different adverse-event denominators. It also provides limited detail on the adverse-event follow-up period and event characteristics.

These limitations concern reporting completeness and interpretation, not a recalculation of the posted arm counts. They should be kept distinct from the sampling uncertainty represented by the reported intervals.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase 3 Study of OTO-201 in Acute Otitis Externa — NCT02801370.
• Registry record last updated 2020-10-19; status last verified 2020-09.
• Results first posted 2020-09-22.
• 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

The registry describes a completed, randomized, double-blind, sham-controlled, multicenter Phase 3 study of a single administration identified in the summary and arm results as 12 mg OTO-201. Enrollment is recorded as 262. The primary endpoint is clinical cure, with posted counts of 91 of 130 in the OTO-201 arm and 63 of 130 in control. The posted risk ratio is 1.444, with an interval from 1.171 to 1.782, and the unadjusted p-value is <0.001.

The record also posts a Day 15 clinical-cure outcome with the same general direction, plus descriptive adverse-event counts. Interpretation is limited by the Day 8 versus Day 15 primary endpoint description, inconsistent intervention naming, and missing details on analysis methods, missing data, and multiplicity. The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification or observed power.