Multiple-Site Study to Evaluate the Therapeutic Equivalence of Permethrin Cream, 5% in the Treatment of Scabies: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Multiple-Site Study to Evaluate the Therapeutic Equivalence of Permethrin Cream, 5% in the Treatment of Scabies (NCT03178942), a randomized phase 3 study. The primary outcome is Number of Patients in Each Treatment Group With Therapeutic Cure (Parasitological Cure Plus Clinical Cure) of Scabies.

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, parallel-design, multiple-site study sponsored by Encube Ethicals Pvt. Ltd. It compared Permethrin Cream, 5% (Encube Ethicals), with Elimite Cream (permethrin) 5% (Prestium Pharma, Inc.) for the treatment of scabies. The record lists the trial as completed, with a start date of 2017-06-01 and a primary completion date of 2017-11-11. It reports enrollment of 254 participants.

Randomized allocation means that assignment to study groups was intended to be determined by chance. A parallel design means that participants were assigned to a treatment group for comparison rather than being described as crossing from one treatment to another. The record calls the study double-blind in its official title and lists masking as quadruple. It does not identify which roles were masked or explain the masking procedures. The number of sites and the allocation ratio are not reported in the registry record.

The primary outcome was therapeutic cure at Day 28 ± 4, analyzed in the PP population. The registry lists 119 participants in the reference group and 117 in the test group for this outcome. These are the denominators used with the outcome counts, and they should not be confused with the overall enrollment figure. The record does not explain how participants were classified into the PP population or how participants without an evaluable primary outcome were handled.

The official title states that the study evaluated therapeutic equivalence. However, the registry record does not report the original protocol’s equivalence margin, sample-size justification, or complete statistical analysis plan. Those omissions limit how fully the intended equivalence framework can be assessed from the posted 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.

Before assignment: All eligible patients were randomized at visit 1 and received the study product with instructions for dosing at home.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Per Protocol (PP) population was used for the analysis.

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 Patients in Each Treatment Group With Therapeutic Cure (Parasitological Cure Plus Clinical Cure) of Scabies, measured over Day 28 ± 4.

The primary endpoint was the number of participants in each treatment group with therapeutic cure of scabies at Day 28 ± 4. The registry specifies that the PP population was used for this analysis. A participant counted as cured only if both the parasitological and clinical criteria were met.

Parasitological cure was defined as failure to demonstrate scabies infestation microscopically: no living mites, no viable mite eggs, and no mite fecal matter present. Clinical cure was defined as visual evidence that there were no new lesions and that original lesions had healed. Post-scabietic nodules did not have to be treated as new lesions or as persistence of old lesions under the stated definition.

Combining these criteria makes the endpoint a joint measure: a participant had to meet the specified parasitological and clinical definitions to be counted as having therapeutic cure. The count-based endpoint is useful for comparing the proportion of participants meeting a defined outcome in each group. In general, a clearly specified endpoint helps make a treatment comparison interpretable; the clinical and microscopy-based definitions indicate what counted as cure in this record. The registry record does not report additional endpoint adjudication procedures or details about how assessments were performed.

7. Results Posted in the Registry

• Test: Permethrin Cream, 5%: 73.5% (86/117) versus 69.7% (83/119) on control; risk difference 3.8 percentage points (95% CI -7.7 to 15.2), risk ratio 1.05 (0.90–1.24); unadjusted two-proportion z-test p = 0.522.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the risk difference express?

The primary comparison is expressed as a risk difference, with the test group compared against the reference group. In general, a risk difference subtracts the event probability in the comparator group from the event probability in the test group. A value of zero corresponds to equal observed event probabilities on this scale. Positive values indicate a higher observed event probability in the test group; negative values indicate a lower one. The posted risk difference is 0.038, and its 95% confidence interval is -0.077 to 0.152.

The risk difference is an absolute measure rather than a relative one. It describes the separation between group probabilities on the probability scale. The registry record also lists a risk ratio and an odds ratio, which describe the same comparison using different scales. Measures can look numerically different because their definitions differ; the scale should be considered when interpreting each estimate.

How should the confidence interval be understood?

In general, a confidence interval gives a range of values compatible with the observed data under the method’s assumptions. It reflects uncertainty in the estimate; it is not a range containing a known treatment effect with certainty. A narrower interval indicates greater precision, while a wider interval indicates less precision. The interval for the risk difference crosses zero, so it includes both directions of difference as well as no difference on that scale. The registry record does not report an equivalence margin against which to evaluate the interval.

What does the p-value tell the reader?

The unadjusted p-value is 0.522. In general, a p-value quantifies how unusual data at least as incompatible with a null hypothesis as those observed would be if that null model and the test assumptions held. It is not a measure of effect size, and it is not the probability that the null hypothesis is true. A p-value alone does not demonstrate equivalence. That conclusion depends on the planned hypotheses, margin, and analysis approach, which are not reported in the registry record.

Why are there several effect measures?

The risk difference, risk ratio, and odds ratio summarize the treatment contrast in different ways. The risk difference uses the subtraction of probabilities; the risk ratio uses their ratio; and the odds ratio compares event odds. In general, the absolute measure can be directly read as a difference on the probability scale, while the relative measures express proportional contrasts. The posted risk ratio is 1.054 with a confidence interval from 0.897 to 1.238, and the posted odds ratio is 1.203 with a confidence interval from 0.682 to 2.121. These are descriptive summaries of the same group outcome data, not independent confirmations.

What does the analysis population mean?

The primary analysis used the PP population. In general, a per-protocol analysis focuses on participants considered to have followed the protocol sufficiently for inclusion under the study’s rules. The exact rules are not reported in the registry record, so it is not possible to determine from this record which deviations affected inclusion. A PP analysis can differ from an analysis based on all randomized participants, especially if inclusion depends on events after randomization. The registry record does not report an intention-to-treat result for this endpoint.

What analysis details are absent?

The registry record lists no posted outcome analysis records, although it includes the group counts and unadjusted comparison summaries discussed in the results. It does not report the full statistical model or test procedure, any adjustment variables, an interim analysis plan, or the handling of missing outcomes. It also does not report the protocol’s equivalence margin or original sample-size justification. These are important details for assessing whether the reported comparison addresses the study’s stated therapeutic-equivalence objective.

In general, analyses of binary outcomes can be affected by the chosen scale, population, missing-data method, and assumptions about the data. The risk difference is the principal scale in this record, but the available information does not allow a full reconstruction of the analysis plan. The posted numerical summaries can be interpreted as unadjusted group comparisons; they should not be treated as evidence that unreported adjustment or design procedures were used.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.038, and its 95% confidence interval ranges from -0.077 to 0.152. The interval is important because the point estimate alone does not convey how uncertain the group contrast is. It extends to both negative and positive values and includes zero. Thus, the posted data do not pin down the direction of the difference with precision on the risk-difference scale.

In general, a confidence interval represents values reasonably compatible with the data and the assumptions of the calculation. It is not a guarantee that the true effect lies within its limits, and it does not show that all values within the interval are equally plausible. The breadth of an interval is one way to assess precision: a wider interval leaves more uncertainty about the size and direction of the effect.

The other reported intervals also reflect uncertainty. The risk ratio is 1.054, with an interval from 0.897 to 1.238; the odds ratio is 1.203, with an interval from 0.682 to 2.121. Each is on a different scale, so their numeric ranges should not be compared directly with the risk-difference interval. The confidence intervals for these relative measures include their null value, as the risk-difference interval includes zero.

For an equivalence question, precision must be interpreted in relation to a prespecified equivalence margin. The registry record does not report such a margin. Without it, the interval cannot be judged against the study’s intended acceptable range of differences. The unadjusted p-value of 0.522 does not substitute for that assessment. The outcome denominators are the PP denominators, and the record does not describe missing-data handling or the analysis population rules; those omissions also limit assessment of precision and robustness.

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, not the trial’s original design calculation. The stated 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 trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm in a hypothetical planning calculation designed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These percentages describe the operating characteristics of hypothetical future study designs under the stated model assumptions; they are not probabilities that the observed result is correct. This is not observed power.

The rows use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For example, the row for planning for 75% of the observed effect lists 4,059 participants per arm for 80% power and 5,433 participants per arm for 90% power. The figures are not the enrollment targets of this trial, and they do not show that the trial achieved the stated power.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants under the same assumptions. The listed figures should be read as sensitivity illustrations: they show how a hypothetical planning requirement changes when the target effect is varied. The record does not report the equivalence margin or other original design assumptions needed to determine whether these illustrations match the trial’s intended design.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.697; treatment proportion p₁ = 0.735; average p̄ = 0.716.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6375 = 1.2496.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6370 = 0.5361.
4. n = (1.2496 + 0.5361)² / (0.0376)² = 2,259.8, rounded up to 2,260 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 <- 0.697478991596639                          # control proportion
p1 <- 0.735042735042735                          # 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(3178942)
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 = 2,260 (80% power), 3,025 (90% power)
 75% of observed effect: n per arm = 4,059 (80% power), 5,433 (90% power)
 50% of observed effect: n per arm = 9,220 (80% power), 12,342 (90% power)
power.prop.test: 2259.8 
Simulated power at n = 2,260 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures and no posted secondary outcome results. It also lists no outcome analysis records. The primary result is available as group counts and unadjusted comparison summaries, but the record does not provide a complete analysis plan describing how all outcomes were to be evaluated.

Multiplicity arises in general when several outcomes, comparisons, time points, or analyses are examined. Repeated testing can increase the chance of at least one apparently unusual result, so a prespecified plan may describe which outcomes are primary and whether or how statistical testing is adjusted. The registry record does not report a multiplicity adjustment plan. It is therefore not possible to tell whether any adjustment was planned or applied. The unadjusted p-value should be interpreted as an unadjusted result, not as evidence that multiplicity was addressed.

The primary endpoint is reported for the PP population. The record does not provide the criteria used to define that population, an intention-to-treat analysis, or a comparison between analysis populations. It does not explain whether all randomized participants were included in the primary analysis or why any might have been excluded.

Missing-data handling is also not reported in the registry record. There is no description of how unavailable or unevaluable primary outcome assessments were treated, whether missingness differed between groups, or whether sensitivity analyses were conducted. In general, the way missing outcomes are handled can affect an estimate, especially if the likelihood of missingness is related to outcome status or treatment group. Without those details, the posted PP result cannot be independently assessed for sensitivity to missing data.

The registry record does not report interim analyses, a detailed statistical analysis plan, or the trial’s original sample-size justification. These missing details do not alter the reported counts, but they limit assessment of the broader analysis strategy and of how closely the posted results correspond to the original plan.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: left foot cellulitus (0.8%).

The safety figures use the safety populations stated for adverse events, rather than the PP denominators used for the primary efficacy outcome. In the reference group, 0 serious adverse events were reported among 129 participants at risk; in the test group, 1 was reported among 125 participants at risk. The record reports 0 deaths in each group.

The registry also reports 7 participants affected by other adverse events in each group, using the stated at-risk populations. A serious adverse event term, Left Foot Cellulitus, is listed with 0.8%. The record does not give further details about the event, its course, or a treatment-group attribution for that term, so the term should not be interpreted beyond the registry listing.

In general, event counts provide a description of what was reported in the recorded safety populations. They do not by themselves establish whether an event was caused by a treatment or allow broad conclusions about comparative safety. Rare events are especially difficult to characterize from a single study’s counts. The safety figures should be read as descriptive registry data, with the limitations of the available event detail and follow-up information.

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

The result describes therapeutic-cure counts under the registry’s stated combined definition and within the PP population. It reports 86 cures among 117 participants in the test group and 83 among 119 in the reference group, with a risk-difference estimate of 0.038. The 95% confidence interval, -0.077 to 0.152, indicates that the estimated contrast is imprecise and includes values on both sides of zero.

These results do not establish that the treatments are equivalent. A formal equivalence assessment requires a margin specified in advance and an analysis that determines whether the confidence interval is contained within that margin. The margin and formal equivalence analysis are not reported in the registry record. A non-significant unadjusted p-value of 0.522 is not proof of equivalence, and failure to establish a difference is not the same as establishing that differences are acceptably small.

The findings also do not show that either treatment is effective or ineffective in a broader population. The posted comparison is limited to this study’s participants, endpoint definition, analysis population, and observation timeframe. The registry record does not provide enough information about eligibility, missing outcomes, PP population rules, or the full analysis plan to assess how those features may affect interpretation.

The safety counts are similarly descriptive. The registry reports 0 serious adverse events in the reference group and 1 in the test group, with 0 deaths in each group. Such counts do not by themselves establish a causal relationship or a general comparative safety profile. No medical recommendation follows from these data alone.

The most defensible reading is therefore narrow: the record reports group outcome counts and an unadjusted comparison at Day 28 ± 4, with uncertainty that includes both directions of difference. The record does not contain the design and analysis details needed to convert that comparison into a formal conclusion about therapeutic equivalence.

16. Why This Trial Matters Statistically

This trial is statistically notable because its stated objective is therapeutic equivalence, while the posted primary comparison is an unadjusted risk difference with a confidence interval that crosses zero. Equivalence is not demonstrated merely because a conventional test does not detect a difference. The key statistical question is whether the plausible differences are sufficiently restricted by a prespecified equivalence margin. The registry record does not report that margin or a formal equivalence analysis.

The example also illustrates why an estimate and its uncertainty should be read together. The point estimate, 0.038, is only one part of the result. The interval from -0.077 to 0.152 leaves uncertainty about both direction and magnitude. A p-value of 0.522 cannot resolve that uncertainty or replace the missing equivalence criterion.

Population definitions also matter. The primary result is based on the PP population, but the registry does not define the rules for inclusion or report an intention-to-treat result. In general, different analysis populations can answer different questions and may yield different estimates. For equivalence trials in particular, understanding the analysis populations and protocol adherence is important to interpreting whether the comparison is robust.

Finally, the planning illustrations show how sample-size requirements depend on the target effect and desired power under stated assumptions. They are not the original study’s design calculation. Without the original margin and sample-size rationale, these illustrations cannot establish whether the trial was designed with adequate precision for its stated objective. The record is therefore useful for teaching the distinction between a non-significant difference and a supported equivalence conclusion, as well as the importance of reporting analysis details.

17. 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 reporting gaps limit interpretation. The registry record does not report the equivalence margin, the original sample-size justification, or the complete statistical analysis plan. As a result, it is not possible to assess whether the study’s design and analysis were tailored to a particular acceptable difference between treatments.

The primary analysis used the PP population, but the record does not give the criteria for that population, explain exclusions, or provide an intention-to-treat result. It also does not report how missing or unevaluable primary outcomes were handled. These omissions make it difficult to assess the influence of protocol deviations, exclusions, or missing outcomes on the primary comparison.

The record lists four outcome measures but no posted secondary outcome results and no posted outcome analysis records. It does not describe any multiplicity approach, interim analysis, or adjustment variables. The available comparison is unadjusted, and the record does not provide enough detail to reconstruct all analytic choices.

Additional design details are limited: the number of sites, allocation ratio, masking procedures, eligibility criteria, and the specific roles covered by quadruple masking are not reported. Although the study is described as randomized, double-blind, parallel, and multiple-site, the registry record does not supply further operational detail about these features.

The primary endpoint has defined clinical and parasitological components, but assessment and adjudication procedures beyond those definitions are not reported. Safety reporting is also limited to the listed counts and term; the record does not provide fuller descriptions of serious-event course or attribution. These limitations do not invalidate the posted results, but they restrict the conclusions that can be drawn from the registry record alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Multiple-Site Study to Evaluate the Therapeutic Equivalence of Permethrin Cream, 5% in the Treatment of Scabies — NCT03178942.
• Registry record last updated 2019-03-26; status last verified 2019-02.
• Results first posted 2019-03-14.
• 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.

21. Record Summary

NCT03178942 is a completed Phase 3 randomized, double-blind, parallel-design, multiple-site study sponsored by Encube Ethicals Pvt. Ltd. It compared Permethrin Cream, 5% (Encube Ethicals), with Elimite Cream (permethrin) 5% (Prestium Pharma, Inc.) for scabies. The registry reports enrollment of 254 participants and lists dates from 2017-06-01 to primary completion on 2017-11-11.

The primary endpoint was therapeutic cure at Day 28 ± 4, defined by parasitological cure plus clinical cure and analyzed in the PP population. The test group had 86 cures among 117 participants; the reference group had 83 among 119. The unadjusted risk difference was 0.038, with a 95% confidence interval from -0.077 to 0.152 and an unadjusted p-value of 0.522. The registry record does not report an equivalence margin or formal equivalence analysis, so the posted comparison alone does not establish equivalence.