Comparative Efficacy and Safety of Ciprofloxacin 0.3% and Dexamethasone 0.1% in Acute Otitis Externa: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Efficacy and Safety of Ciprofloxacin 0.3% and Dexamethasone 0.1% in Acute Otitis Externa (NCT02216071), a randomized phase 3 study. The primary outcome is Number of Participants With Clinical Cure of AOE.

2. Clinical Question

This is an active-comparator question: the registry describes a comparison between two otic suspensions, rather than a comparison with no treatment or a placebo. The primary outcome counts participants classified as having clinical cure. For subjects with AOE in both ears, cure required a score of 0 for both ears.

The posted results record clinical cures in both arms. They also give an unadjusted comparison and a confidence interval for the risk difference. Those estimates describe the observed comparison, but a formal non-inferiority conclusion depends on a prespecified non-inferiority margin and an appropriate analysis plan. The margin and the trial’s detailed statistical plan are not reported in the registry record, so the stated objective cannot by itself establish that the formal criterion was met.

3. Trial Design

The registry record describes a Phase 3, randomized, double-blind, active-controlled, parallel-group study. It reports quadruple masking. The record identifies the sponsor as Exela Pharma Sciences, LLC. Enrollment was 499. The study status is completed, with a start date of 2014-07-20 and primary completion date of 2015-08-11.

The two groups received either EXL CDOS or Ciprodex®, the reference-listed drug. Both were otic suspensions administered twice daily for 7 days. The registry’s brief summary states that the study aimed to demonstrate clinical therapeutic non-inferiority of EXL CDOS to commercially available Ciprodex® in treating acute otitis externa.

The primary endpoint was assessed 7 days after completion of therapy, at Day 15 (+/- 1 day). The primary result lists 254 participants and 190 clinical cures for Ciprodex®, and 245 participants and 191 clinical cures for EXL CDOS. The registry record does not report the analysis population associated with these counts or explain how participants without an endpoint assessment were handled.

Randomization and masking describe important design features, but they do not supply all details needed to assess risk of bias or reproduce the analysis. The method used to generate the allocation sequence, conceal allocation, implement masking, and maintain masking is not reported in the registry record. Nor are protocol details such as eligibility criteria, site procedures, or the original sample-size justification 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.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Clinical Cure of AOE, measured over 7 days after the completion of therapy; at Day 15 (+/- 1 day).

The primary endpoint counts participants with clinical cure of acute otitis externa. Cure was defined as a clinical AOE score of 0 at the test-of-cure visit. For a participant with AOE in both ears, both ears had to have a score of 0.

The score combined assessments of inflammation, edema, tenderness, and otorrhea. Inflammation and edema were graded from absent through severe; tenderness and otorrhea were recorded as absent or present. The endpoint therefore reduces several clinical signs and symptoms to a binary classification: cured or not classified as cured under the stated definition.

A clinical-cure endpoint is useful for a treatment comparison because it represents a clinically defined status at a specified follow-up visit. It is distinct from a microbiological-cure endpoint, which concerns microbiological findings rather than the clinical score. The primary endpoint was assessed 7 days after completion of therapy, at Day 15 (+/- 1 day), allowing the comparison to focus on status after the treatment course rather than during administration.

Like any binary endpoint, this measure depends on the definition and assessment of cure, the timing of the visit, and how missing assessments are handled. The registry record gives the score definition and assessment timing, but does not report the missing-data rules or the detailed procedures used to evaluate the signs and symptoms.

7. Results Posted in the Registry

• EXL CDOS: 78.0% (191/245) versus 74.8% (190/254) on control; risk difference 3.2 percentage points (95% CI -4.3 to 10.6), risk ratio 1.04 (0.95–1.15); unadjusted two-proportion z-test p = 0.407.

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 Participants With Microbiological Cure (MC)

• 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:
  • EXL CDOS: 78.5% (117/149) versus 71.9% (115/160) on control; risk difference 6.6 percentage points (95% CI -2.9 to 16.2), risk ratio 1.09 (0.96–1.24); unadjusted two-proportion z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EXL CDOS and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint, microbiological cure, assessed at the same stated follow-up timing as the primary endpoint. The direction of its posted comparison favors EXL CDOS, which is consistent with the direction of the primary risk-difference estimate. The interval for this secondary comparison includes no difference, and the record lists no reported analyses for the endpoint.

This pattern adds descriptive context but does not provide a separate, definitive confirmation of the primary result. Microbiological cure concerns a different outcome from clinical cure, and a favorable direction alone does not establish that the effect is reliable or clinically important. Its interpretation also depends on whether the endpoint, analysis, and handling of missing data were prespecified and consistently applied; those details are not reported in the registry record.

Unadjusted secondary results generally carry less weight than a primary analysis because researchers may assess multiple outcomes, increasing the chance that at least one result appears notable by chance. General explanation: multiplicity methods or a prespecified testing hierarchy can help control this issue, but neither is described in the registry record. The secondary result should therefore be considered supportive context, not a stand-alone basis for a conclusion about the study’s non-inferiority objective.

The registry does not report additional secondary analyses that would allow a broader assessment across outcomes. The posted secondary evidence is limited to this one endpoint and its unadjusted comparison. It should be interpreted alongside the primary result, while keeping the distinction between clinical cure and microbiological cure clear.

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

• Number of Participants With Microbiological Cure (MC)

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint such as clinical cure, each participant is classified as having or not having the event. The posted counts show the number classified as cured and the number included in each arm’s endpoint denominator. A treatment comparison can then be expressed using quantities such as a risk difference, risk ratio, or odds ratio. These are different ways to describe the relationship between the observed event proportions.

What does the risk difference describe?

The risk difference is the observed event proportion in one arm minus the observed event proportion in the comparator arm. A value of zero represents no difference in the proportions. A positive value in this comparison points toward a higher observed cure proportion for EXL CDOS; a negative value points toward a higher observed cure proportion for Ciprodex®. The posted estimate points in the positive direction, while its confidence interval spans zero.

That estimate is unadjusted: it does not account for covariates or other model adjustments. An unadjusted comparison can be straightforward to interpret, but it does not reveal whether the trial used adjusted analyses elsewhere. Such analyses are not reported in the registry record. The posted unadjusted p-value is 0.407. A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure clinical importance.

How should a confidence interval be understood?

In general, a confidence interval expresses uncertainty around an estimate using a method with a stated long-run coverage property. For this risk difference, the interval includes zero, so the posted data do not rule out no difference using the interval as reported. It also extends in the direction of a positive difference. The interval should be considered alongside the point estimate, rather than treated as a second result or a boundary of every effect that could be possible.

A confidence interval and a p-value are related summaries of uncertainty, but they answer different practical questions. The interval shows a range of effect estimates compatible with the data under the method used. The p-value summarizes evidence against a null value under a specified test. Neither one determines whether a difference is clinically important. That assessment would require a clinical threshold, which is not reported in the registry record.

Why is the non-inferiority objective important?

General explanation: a non-inferiority trial asks whether the experimental treatment is not worse than its active comparator by more than a prespecified acceptable amount. This is not the same as asking whether a conventional test detects a difference. The non-inferiority margin and the analysis conventions must be set in advance and interpreted in the context of the trial’s design. The registry record states a non-inferiority objective but does not report the margin, the original sample-size assumptions, or a detailed analysis plan. Without those details, the posted risk difference and interval cannot be judged against a formal non-inferiority threshold.

Non-inferiority assessment can also depend on the analysis population and how protocol deviations and missing outcomes are handled. If those rules are not known, it is difficult to assess whether the analysis matches the intended question. The registry record does not report the analysis populations, missing-data methods, or sensitivity analyses for the primary outcome.

What does the secondary endpoint add?

The registry posts one secondary endpoint: microbiological cure. It gives group counts and an unadjusted comparison, but lists no reported analyses. General explanation: secondary endpoints may help describe different aspects of an outcome, but their interpretation is affected by how many outcomes were tested and whether an analysis plan controlled the chance of false-positive findings. The registry record does not report a multiplicity strategy or an endpoint hierarchy. The secondary result therefore should not be treated as equivalent to a prespecified, multiplicity-controlled primary finding.

Finally, all statistical summaries depend on the quality and completeness of the underlying outcome assessments. The registry provides endpoint counts and a comparison, but does not report detailed assessment procedures, missing-data rules, or adjusted models. These omissions limit how fully the posted results can be independently evaluated.

11. Confidence Intervals and Precision

The primary risk-difference confidence interval extends from a value below zero to a positive value. Because zero lies within the interval, the posted data are compatible with no difference as well as with effects favoring either arm over some part of the interval. The interval is therefore important context for the positive point estimate: the estimate alone gives a less complete account of uncertainty.

The unadjusted p-value of 0.407 is consistent with the interval not excluding zero. It does not show that the arms are equivalent, and it does not establish non-inferiority. Equivalence and non-inferiority require their own prespecified margins and decision criteria. The registry record does not report the non-inferiority margin or detailed criteria for evaluating it.

Precision refers to how narrowly the effect is estimated, not to whether the result is clinically important or unbiased. A broad interval allows a wider range of effects to remain compatible with the data; a narrower interval constrains that range more closely. Even a precise estimate can be affected by bias or by limitations in outcome measurement, while an imprecise estimate may leave a clinically relevant difference unresolved.

The registry reports a risk difference as its main comparison and also supplies relative-effect summaries. Those measures use different scales and should not be treated as interchangeable. The central point for interpretation is that the primary interval crosses the no-difference value. The result is not precise enough to establish that the groups have identical outcomes, and the registry information does not permit a formal assessment of non-inferiority.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculation. Each row considers planning for a stated fraction of the observed effect. The table gives participants per arm for 80% power and participants per arm for 90% power. These are per-arm figures, not total enrollment and not total events.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

In general, power is the probability that a specified statistical procedure will detect an effect of a specified size under its assumptions. The 80% power column illustrates the number of participants per arm under which the planning method would have an 80% chance of detecting the chosen effect, if that effect and the assumptions were correct. The 90% column uses a higher target probability of detection and consequently requires a larger planned sample for the same effect. Smaller effects need more participants to detect than larger effects, all else equal.

These figures are not observed power. They do not measure the probability that the posted trial result is true, nor do they show that the trial was designed with those sample sizes. Because the calculation uses the observed effect as its starting point, it is a planning illustration rather than evidence about the trial’s original planning or the certainty of its result.

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 = 0.748; treatment proportion p₁ = 0.780; average p̄ = 0.764.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6007 = 1.1773.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6003 = 0.5052.
4. n = (1.1773 + 0.5052)² / (0.0316)² = 2,842.0, rounded up to 2,842 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 <- 0.748031496062992                          # control proportion
p1 <- 0.779591836734694                          # 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(2216071)
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 = 2,842 (80% power), 3,805 (90% power)
 75% of observed effect: n per arm = 5,112 (80% power), 6,842 (90% power)
 50% of observed effect: n per arm = 11,630 (80% power), 15,569 (90% power)
power.prop.test: 2842 
Simulated power at n = 2,842 per arm: 0.797 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a detailed statistical analysis plan, a hierarchy for testing endpoints, or a method for adjusting for multiple comparisons. It also does not report whether there were interim analyses or any prespecified rules for stopping or changing the study. These details are important for understanding how confirmatory conclusions were intended to be reached.

Multiplicity arises when several hypotheses or outcomes are evaluated. General explanation: the more opportunities there are to declare a finding, the greater the chance of a false-positive result unless the testing strategy accounts for this. A prespecified hierarchy or adjustment can help define how primary and secondary outcomes contribute to conclusions. Since the registry posts one secondary endpoint and no reported analyses, the record does not establish how that endpoint was positioned in the overall testing strategy.

The registry also does not report the analysis populations for the primary or secondary outcomes. In a non-inferiority study, the choice and definition of analysis populations can matter, as can the treatment of protocol deviations. The record does not describe an intention-to-treat population, a per-protocol population, or how participants were included in the posted endpoint denominators.

Missing-data methods are not reported in the registry record. It is therefore unclear how absent test-of-cure assessments, withdrawals, or other unavailable outcomes were handled. The registry does not report sensitivity analyses exploring how different assumptions about missing outcomes might affect the comparison. These omissions limit the ability to evaluate whether the observed result is robust to incomplete follow-up.

The registry states the non-inferiority objective, but the margin and the original sample-size assumptions are not reported. Without them, the posted estimates cannot be assessed against the trial’s intended decision rule. The registry record also does not report whether the sponsor’s analysis included adjustments or additional analyses beyond the posted summaries.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: tmj syndrome (0.4%).

The serious adverse event figures list 0 serious adverse events among 247 participants at risk in the Ciprodex® group and 1 among 252 participants at risk in the EXL CDOS group. These are event counts and the corresponding denominators reported for the safety summaries. The registry also lists TMJ Syndrome at 0.4% among the top serious terms.

These figures are descriptive. A difference in the number of serious adverse events does not by itself establish a treatment-related safety difference, particularly when event counts are small. The registry record does not report the details needed to assess causality, timing, severity criteria, or whether the listed serious event was considered related to treatment.

Deaths are not reported in the registry record. The serious adverse event counts should not be read as a complete account of all possible harms: the record also lists other adverse events, but the summary above concerns serious adverse events specifically. The reported figures describe what was recorded in the safety summary and do not establish comparative safety beyond those data.

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

The posted data show clinical cures in both treatment groups, with the risk-difference estimate pointing toward a higher observed cure proportion for EXL CDOS. The confidence interval includes no difference, and the unadjusted p-value is 0.407. These results do not demonstrate that the treatments are identical, and they do not by themselves establish that EXL CDOS met a non-inferiority criterion.

The distinction matters because a non-inferiority conclusion depends on a prespecified margin and a suitable analysis, not simply on failing to detect a conventional statistical difference. The registry record states the non-inferiority objective but does not report the margin, the original statistical plan, or the analysis populations. As a result, the formal meaning of the observed estimate against the intended criterion cannot be determined from the registry information alone.

The microbiological-cure outcome provides a secondary perspective, but it does not replace the primary clinical endpoint. Its direction is consistent with the primary estimate, while its uncertainty and the absence of reported multiplicity methods limit the weight it can carry. The safety summary reports few serious adverse events in the groups, but those counts alone do not establish a comparative safety profile.

More broadly, trial results apply most directly to the participants, setting, outcome definitions, and follow-up represented in the study. The registry record does not provide detailed eligibility criteria, missing-data procedures, or enough information to assess all aspects of generalizability. The findings should therefore be read as a record of the posted outcomes and their uncertainty, not as a guarantee of an outcome for an individual or as a complete characterization of benefits and harms.

17. Why This Trial Matters Statistically

This trial illustrates why the statistical question must match the study objective. A conventional comparison asks whether the data provide evidence of a difference under a null hypothesis. A non-inferiority study asks whether the experimental treatment’s outcome is not worse than the comparator by more than a prespecified margin. Those are related but distinct questions, and the same point estimate cannot answer both without the relevant decision criteria.

The posted primary estimate is positive in the direction of EXL CDOS, but the confidence interval includes no difference. This makes precision central to interpretation: the point estimate alone does not capture the range of effects compatible with the data. The missing non-inferiority margin and analysis details further limit what can be concluded from the registry record about the stated objective.

The record also illustrates the role of endpoint definitions. Clinical cure is based on a composite clinical score, whereas microbiological cure is a separate secondary outcome. Different endpoints can describe different aspects of a condition, but their results should not be combined into a single claim without a prespecified rationale and a suitable analysis.

Finally, the sample-size illustrations are not the original design calculation. They show how planning requirements vary with the chosen effect and power target under listed assumptions, while leaving the trial’s own design rationale unreported. Taken together, these features show why effect estimates, uncertainty, endpoint hierarchy, and design assumptions need to be considered together when reading a clinical trial record.

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 trial-specific details needed for a full appraisal are not reported in the registry record. These include the non-inferiority margin, the original sample-size justification, the detailed statistical analysis plan, and the analysis populations used for the posted outcomes. Without the margin and analysis conventions, the formal non-inferiority conclusion cannot be evaluated from the posted summary alone.

The record does not describe how missing primary or secondary outcome assessments were handled, nor does it report sensitivity analyses for missing data. It also does not provide detailed eligibility criteria or explain how participants with protocol deviations were treated in the analyses. These gaps limit assessment of the stability and applicability of the outcome comparisons.

The registry identifies the study as randomized, double-blind, and quadruple-masked, but does not describe the allocation-generation or allocation-concealment procedures, or how masking was implemented. The record does not report whether interim analyses occurred, or whether any stopping rules were used.

The primary comparison is posted as an unadjusted analysis. Adjusted analyses are not reported in the registry record. The secondary endpoint has no reported analyses, and a multiplicity strategy is not described. Safety summaries list serious event counts, but the record does not provide details sufficient to assess causality or the completeness of event ascertainment. These are limitations of the information available in the registry record and do not, by themselves, establish that the trial procedures were inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparative Efficacy and Safety of Ciprofloxacin 0.3% and Dexamethasone 0.1% in Acute Otitis Externa — NCT02216071.
• Registry record last updated 2021-05-28; status last verified 2020-09.
• Results first posted 2021-05-28.
• 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

NCT02216071 is a completed Phase 3 randomized, double-blind, active-controlled, parallel-group study of EXL CDOS and Ciprodex® for acute otitis externa. Both otic suspensions were administered twice daily for 7 days. The registry reports enrollment of 499 and primary completion on 2015-08-11.

The primary endpoint was clinical cure at the test-of-cure visit, defined as a clinical AOE score of 0. The posted risk-difference estimate favors EXL CDOS, but its confidence interval includes no difference; the unadjusted p-value is 0.407. The registry states a non-inferiority objective but does not report the margin or detailed statistical plan needed to evaluate that objective formally.

One secondary endpoint, microbiological cure, is posted without reported analyses. Serious adverse event counts are low in both groups, and the registry does not report deaths. Missing-data methods, analysis populations, and multiplicity procedures are not reported in the registry record.