A Study Evaluating the Safety and Efficacy of BGC20-0582 Lice Treatment Gel for Head Lice Infestation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Evaluating the Safety and Efficacy of BGC20-0582 Lice Treatment Gel for Head Lice Infestation (NCT00528021), a randomized phase 2 study. The primary outcome is Clinical Cure.

2. Clinical Question

3. Trial Design

The registry record identifies this as a randomized, double-masked, parallel Phase 2 study. Enrollment was 230. The study status is completed; the recorded start was 2007-08 and primary completion was 2008-05. Boston Scientific Corporation is listed as the sponsor. These design labels describe the broad structure of the trial, but the registry record does not give the randomization procedure, allocation ratio, concealment method, or details about how masking was maintained.

The intervention descriptions identify topical BGC20-0582 at 2.5%, 10%, and 12.5%, with vehicle as comparator. The record says participants received treatment either once on day 1 or twice on day 1 and day 7, followed by rinsing the product from the hair. It does not specify which participants or concentrations followed each schedule, or explain whether schedule was itself assigned or analyzed as a separate factor. The arm description for one listed arm is blank, so the registry record does not resolve every aspect of the arm structure.

The primary outcome is Clinical Cure, defined as the count of participants with no live lice at Day 15 or 22. Outcome data are posted for three active concentration groups and vehicle. The group sizes for this outcome are 42.0, 46.0, 49.0, and 47.0, respectively. These posted group counts do not account for the full enrollment, and reasons for the difference are not reported in the registry record. The record lists one outcome measure and no posted secondary outcomes. It does not report the trial's original sample-size justification, analysis populations, or detailed statistical analysis plan.

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 Clinical Cure, measured over Day 15 or 22.

The primary endpoint is labeled Clinical Cure and measures the count of participants with no live lice at Day 15 or 22. It is therefore a binary participant-level outcome: each participant is classified according to whether live lice were absent at the stated assessment. The posted result is the number meeting that definition in each treatment group, alongside the group size.

A clinical cure endpoint expresses an outcome in terms of participants meeting a defined condition, rather than a change in a continuous measurement. In general, binary endpoints can be summarized as counts and proportions, and groups can be compared by estimating differences or ratios between those proportions. The specific posted group counts are 30.0 of 42.0 for 2.5% BGC20-0582, 28.0 of 46.0 for 10% BGC20-0582, 35.0 of 49.0 for 12.5% BGC20-0582, and 32.0 of 47.0 for vehicle.

The stated assessment time is Day 15 or 22, rather than a single day for all participants. The registry record does not explain what determined the assessment day, whether the two times corresponded to different treatment schedules, or how outcomes at the two times were combined. That missing detail limits interpretation of the endpoint as a result at one uniform follow-up time. The registry record also does not report a separate definition for handling missing assessments or other deviations from the endpoint definition.

7. Results Posted in the Registry

• 2.5% BGC20-0582: 71.4% (30/42) versus 68.1% (32/47) on control; risk difference 3.3 percentage points (95% CI -15.7 to 22.4), risk ratio 1.05 (0.80–1.38); unadjusted two-proportion z-test p = 0.732.
• 10% BGC20-0582: 60.9% (28/46) versus 68.1% (32/47) on control; risk difference -7.2 percentage points (95% CI -26.6 to 12.2), risk ratio 0.89 (0.66–1.21); unadjusted two-proportion z-test p = 0.467.
• 12.5% BGC20-0582: 71.4% (35/49) versus 68.1% (32/47) on control; risk difference 3.3 percentage points (95% CI -15.0 to 21.7), risk ratio 1.05 (0.81–1.37); unadjusted two-proportion z-test p = 0.721.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is a binary outcome, because each participant either had no live lice at assessment or did not meet that definition. The posted values are participant counts, with each count paired with the group size. In general, a binary outcome can be described by a proportion and compared between groups using a risk difference, risk ratio, or odds ratio. These measures answer related but distinct questions, and each can have its own confidence interval.

What does the risk difference express?

The risk difference is the active-group proportion minus the vehicle-group proportion. Zero indicates equal observed proportions; positive values indicate a higher proportion in the active group, and negative values indicate a lower proportion. The recalculated unadjusted risk differences are 0.033 for 2.5% BGC20-0582, -0.072 for 10%, and 0.033 for 12.5%. These estimates use the posted outcome counts and group sizes directly, without adjustment for other variables. The registry record does not report adjusted estimates, covariates, or a sponsor analysis for the endpoint.

How should ratios be understood?

A risk ratio compares the outcome proportions by division, while an odds ratio compares the odds of the outcome. Values at the null value indicate no relative difference: the null is 1 for a ratio measure. In general, ratios can be less intuitive than a risk difference because they express relative rather than absolute comparison. The recalculated ratios and their intervals are posted for each active group, but all three measures should be interpreted alongside the small group sizes and uncertainty. The registry record does not describe which measure, if any, was selected as the primary comparison in the original statistical plan.

What do a confidence interval and p value add?

A confidence interval communicates the range of estimates reasonably compatible with the data under the statistical method used. It is not a guarantee that the true value lies inside the interval, nor does it indicate the probability that a treatment effect is real. For the recalculated risk differences, the intervals cross zero. This means the intervals include values compatible with no difference as well as values on either side of no difference. A p value measures how unusual results at least as discrepant as those observed would be under a specified null model and its assumptions. It does not measure the size or importance of an effect. The unadjusted p values are 0.732, 0.467, and 0.721 for the three active-group comparisons, respectively.

Why does the distinction between recalculation and trial analysis matter?

The numerical comparisons are labeled recalculated because they are simple unadjusted calculations from the posted summary counts. They do not establish that the trial investigators used the same statistical method or considered the same analysis population. The registry record reports no posted analyses, and the analysis plan, adjustment strategy, and handling of missing outcomes are not reported in the registry record. In general, adjusted methods can account for prespecified covariates or features of the design, while simple comparisons of group summaries do not. If the trial's own analysis differs, its interpretation would depend on its methods and assumptions; those details are not available in the registry record.

What is over-dispersion, and does it apply?

Over-dispersion is a general concern in count models when the observed variation exceeds what a model assumes. It can make model-based uncertainty too small if not handled appropriately. The primary outcome is reported as participant counts for a binary endpoint, not as an event rate modeled over person-time. No count-model analysis or over-dispersion assessment is reported in the registry record, so over-dispersion cannot be assessed from the posted results. More generally, model choice should match how the outcome was measured and the trial design.

The registry record identifies randomization, double masking, and a parallel design, but does not report the randomization method, the allocation ratio, or methods for addressing departures from the intended design. The record also does not report an original sample-size justification, interim analyses, a statistical analysis plan, or a prespecified multiplicity strategy. These are unknowns rather than evidence that a particular method was or was not used. The recalculated summaries are useful for describing the posted counts, but they cannot substitute for those missing protocol and analysis details.

10. Confidence Intervals and Precision

The confidence intervals around the recalculated risk differences are broad and include zero for each comparison with vehicle. In general, a confidence interval summarizes the uncertainty in an estimate under the calculation method. When an interval for a risk difference includes zero, the posted data are compatible with no difference as well as with differences in either direction. Here, the recalculated comparisons yield risk differences of 0.033 for 2.5% BGC20-0582, -0.072 for 10%, and 0.033 for 12.5%; their intervals all extend across zero.

The intervals are based on groups of 42.0, 46.0, and 49.0 participants in the active groups and 47.0 participants in vehicle. With group sizes of this scale, a few participant outcomes can materially affect the estimated proportions. That general feature of binary outcomes is one reason to avoid treating the point estimates as precise rankings of the concentrations. The intervals do not establish that all clinically relevant differences are absent; they show that the recalculated estimates are uncertain and compatible with a range of possibilities.

Precision is distinct from whether a result meets a statistical threshold. A narrow interval would indicate greater statistical precision, while a broad interval indicates more uncertainty about the magnitude and direction of the difference. The registry record does not identify a prespecified analysis or decision threshold, and the recalculated intervals should not be interpreted as a substitute for the trial's original statistical analysis. The outcome assessment is reported at Day 15 or 22; the record does not explain the timing distinction, which further limits how precisely the results can be interpreted as applying to one follow-up point.

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 sample-size figures are planning illustrations based on the observed effect in each active-group comparison, not the trial's original design assumptions. The original sample-size justification and its assumptions are not reported in the registry record. These illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show the participants per arm for 80% power and participants per arm for 90% power, with the effect to detect set at 100%, 75%, or 50% of the observed effect.

For example, using 100% of the observed effect, the illustration for 2.5% BGC20-0582 gives 2,962 participants per arm for 80% power and 3,964 per arm for 90% power. The corresponding illustration for 10% gives 690 and 923 participants per arm. These are hypothetical future planning values under the stated assumptions, not counts enrolled in this trial. The 80% power column means that a study planned under those assumptions would have an 80% chance of detecting the specified effect at the stated significance level, if that effect were the true effect and the assumptions held. The 90% column describes the analogous plan with a 90% chance under those conditions.

Rows that plan for 75% or 50% of the observed effect target smaller differences. Smaller effects generally require more participants to distinguish them from random variation, so the displayed planning requirements increase as the target effect gets smaller. The illustrations do not say that the completed trial had the stated probability of detecting an effect; this is not observed power. They are conditional planning calculations and should not be used as a retrospective verdict on the trial's performance. The registry record does not report its original design assumptions, and the displayed calculations do not recover them.

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 = 0.681; treatment proportion p₁ = 0.714; average p̄ = 0.698.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6496 = 1.2731.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6491 = 0.5463.
4. n = (1.2731 + 0.5463)² / (0.0334)² = 2,961.3, rounded up to 2,962 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 <- 0.680851063829787                          # control proportion
p1 <- 0.714285714285714                          # 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(528021)
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 = 2,962 (80% power), 3,964 (90% power)
 75% of observed effect: n per arm = 5,307 (80% power), 7,104 (90% power)
 50% of observed effect: n per arm = 12,031 (80% power), 16,105 (90% power)
power.prop.test: 2961.3 
Simulated power at n = 2,962 per arm: 0.798 (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 trial reports three active concentration comparisons against vehicle for the same primary endpoint. When several comparisons are examined, the chance of at least one apparently unusual result can increase if each is assessed separately without accounting for multiplicity. In general, a multiplicity plan may specify which comparisons are confirmatory, how type I error is controlled, and whether a hierarchy or adjustment is used. No such strategy is reported in the registry record. The recalculated p values are unadjusted, so they should not be treated as multiplicity-adjusted evidence.

The registry record lists one outcome measure and zero posted secondary outcomes. That does not establish that no other outcomes were collected or analyzed; it means no secondary outcome results are posted in the record. It also does not establish whether the three concentrations were each designated as confirmatory comparisons or whether one was the principal contrast. The original protocol and statistical analysis plan are not reported in the registry record, so the intended testing hierarchy and any adjustment for multiple comparisons are unknown.

Information about missing outcome data and analysis populations is also not reported. The enrollment is 230, while the posted primary outcome groups contain 42.0, 46.0, 49.0, and 47.0 participants. The registry record does not explain why the outcome group sizes do not cover enrollment, how many randomized participants lacked an assessment, or how missing observations were handled. It does not identify whether the endpoint analysis used an intention-to-treat population, a per-protocol population, or another defined group. These distinctions matter because exclusions or missing observations can affect both the estimated group proportions and the interpretation of randomization.

The recorded assessment is Day 15 or 22, but the registry record does not explain how assessment timing was incorporated into the analysis. It also does not report methods for protocol deviations, repeated observations, or sensitivity analyses. These gaps should be understood as unreported methodological details, not as evidence that a particular analysis was omitted. The available unadjusted calculations describe the posted counts but cannot answer how the original trial analysis addressed multiplicity or missing data.

14. 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 non-serious adverse event terms

The serious adverse event figures report zero affected participants in each group. The denominators at risk are 59 for 2.5% BGC20-0582, 59 for 10%, 56 for 12.5%, and 56 for vehicle. These are safety denominators and differ from the group sizes posted for the primary efficacy outcome. The registry record does not explain the denominator difference, so the safety and efficacy counts should not be assumed to refer to identical analysis populations.

A reported zero means no serious adverse events were recorded among the stated participants at risk in the registry results. It does not prove that the risk is zero or rule out uncommon events; in general, an event that was not observed in a limited group may still occur in a larger population. The registry record lists no serious adverse event terms. Death counts are not reported in the registry record.

Other adverse events are reported for 13 participants in the 2.5% group, 10 in the 10% group, 16 in the 12.5% group, and 11 in vehicle, with the corresponding safety denominators above. These counts are separate from serious adverse events. The registry record does not provide event descriptions in the posted summary or a detailed comparative safety analysis. The counts should therefore be read descriptively and should not be used alone to infer comparative safety.

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

The posted results establish what was recorded for the primary outcome in the four groups: 30.0 of 42.0 participants in the 2.5% group, 28.0 of 46.0 in the 10% group, 35.0 of 49.0 in the 12.5% group, and 32.0 of 47.0 in vehicle had no live lice at Day 15 or 22. The unadjusted recalculated risk differences versus vehicle are small in magnitude in the displayed estimates, and all corresponding confidence intervals include zero. The posted p values are 0.732, 0.467, and 0.721. Together, these summaries convey uncertainty rather than a clear, precise separation between each active group and vehicle.

They do not establish that the groups are identical. An interval that includes zero can reflect limited precision and does not rule out differences in either direction. Nor do the results establish that any concentration is superior or inferior; the registry record does not report a sponsor analysis, a direct comparison among concentrations, or a concentration-response analysis. The observed estimates vary in direction, and the group counts alone cannot tell whether that pattern reflects random variation, differences in treatment schedule, or other factors.

The findings also do not answer questions beyond the recorded endpoint and assessment time. The registry record describes an assessment at Day 15 or 22 but does not clarify how those times were assigned or combined. It does not report long-term outcomes, an analysis of recurrence, or details on missing outcome data. The difference between enrollment and the outcome-group sizes remains unexplained in the registry record.

In general, statistical uncertainty is not a treatment recommendation. These data should be interpreted as a record of outcome counts and imprecise unadjusted comparisons in this completed Phase 2 trial. They cannot, on their own, resolve clinical importance, generalizability, or the full balance of benefits and harms. The registry record's limited analysis details also mean that these recalculations should not be mistaken for the trial investigators' complete statistical conclusions.

16. Why This Trial Matters Statistically

This trial is statistically informative as an example of why a numerical difference and a dependable conclusion are not the same thing. The posted counts produce different point estimates across concentration groups, but the recalculated intervals for each comparison with vehicle include zero and extend in both directions. A point estimate gives one summary of the observed data; the interval indicates how much uncertainty surrounds it. Reporting both is essential when group sizes are modest and the outcome is binary.

The trial also has multiple active concentration comparisons against one vehicle group. That structure raises a general question about multiplicity: whether comparisons were designated in advance and how the overall interpretation was protected from the accumulation of chance findings. The registry record does not report those details. Its three unadjusted recalculated comparisons can illustrate the data, but they do not reveal the study's original testing plan.

Another statistical issue is the distinction between the study's enrollment and the outcome denominators. The primary outcome counts cover fewer participants than the enrollment figure, and the safety denominators are different again. Without an account of analysis populations and missing data, readers cannot determine how those differences arose or whether the same participants contributed to each result. That matters because transparent accounting connects randomization to the analysis that supports an inference.

Finally, the sample-size illustrations show how planning requirements depend on the target effect: smaller effects generally call for larger groups to achieve the same planned power. Those illustrations are not evidence about the design chosen for this trial. Taken together, the record highlights the importance of prespecified methods, complete participant accounting, and reporting uncertainty alongside outcome counts.

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.

The registry record leaves several trial-specific uncertainties. It describes treatment once on day 1 or twice on day 1 and day 7, but does not identify which schedule applied to each concentration or how the schedule was incorporated into the analysis. Since the primary assessment is stated as Day 15 or 22, the relationship between dosing schedule and assessment timing is not clear. The treatment descriptions also do not explain the arm structure in full, and one arm description is blank.

The primary outcome group sizes do not account for the full enrollment. The record does not report why, which participants were excluded or lacked outcomes, or how missing results were treated. The safety denominators are also distinct from the efficacy denominators, without an explanation of the difference. These omissions limit assessment of the analysis populations and the degree to which posted results preserve the randomized comparison.

Only one outcome measure is listed, with no secondary outcomes posted. No sponsor analysis is posted, and no original statistical analysis plan, sample-size justification, interim-analysis information, adjustment strategy, or multiplicity approach is reported in the registry record. The risk differences and p values discussed are simple unadjusted recalculations from the group summaries; they do not account for covariates or clarify whether the original analysis used a different method.

The outcome is recorded at Day 15 or 22 rather than at a single stated assessment day. The record does not explain the timing choice or provide separate results by assessment time. The posted primary results are counts, without detail on participant characteristics or reasons for missing results. These limits make it difficult to assess precision across subgroups or generalize beyond the participants and assessment described. They do not invalidate the posted counts, but they restrict what can be inferred from them.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study Evaluating the Safety and Efficacy of BGC20-0582 Lice Treatment Gel for Head Lice Infestation — NCT00528021.
• Registry record last updated 2022-06-28; status last verified 2022-06.
• Results first posted 2010-12-28.
• 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.

21. Record Summary

The completed Phase 2 study NCT00528021 was a randomized, double-masked, parallel comparison of topical BGC20-0582 gel with vehicle for head lice infestation. Enrollment was 230. The recorded study start was 2007-08 and primary completion was 2008-05. The primary endpoint, Clinical Cure, counted participants with no live lice at Day 15 or 22.

Posted outcome counts were 30.0 of 42.0 for 2.5% BGC20-0582, 28.0 of 46.0 for 10%, 35.0 of 49.0 for 12.5%, and 32.0 of 47.0 for vehicle. Recalculated unadjusted comparisons with vehicle have confidence intervals that include zero. The registry record does not report the original analysis plan, missing-data handling, or explanation for the difference between enrollment and outcome group sizes. Serious adverse event counts were zero in each reported safety group; deaths are not reported in the registry record.