Management of Skin and Soft Tissue Abscesses in Pediatric Patients After Incision and Drainage: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Management of Skin and Soft Tissue Abscesses in Pediatric Patients After Incision and Drainage (NCT00691600), a randomized phase 3 study. The primary outcome is Number of Participants With Abscess Resolution.

2. Clinical Question

The clinical question is therefore about the additional contribution of antibiotic treatment after drainage, rather than a comparison of drainage with no drainage. The registry’s brief summary frames the objective as comparing cure rates with and without antibiotic treatment after incision and drainage. It also identifies secondary outcomes concerning admission for failure of resolution and the need for new or modified antibiotics. The record does not provide further detail about how the clinical decision to use those secondary outcomes was made.

3. Trial Design

The registry identifies this as a Phase 3, randomized study sponsored by Baylor College of Medicine. The record lists an enrollment of 23 and status as completed. It gives a start date of 2007-12 and a primary completion date of 2010-04. These are registry dates and do not, by themselves, describe how long any individual participant was followed.

Allocation is described as randomized and masking as quadruple. The intervention listing includes oral trimethoprim/sulfamethoxazole and placebo. The arm descriptions say that subjects with abscesses less than 5 cm were randomized to study medication or placebo, and that the placebo was given after incision and drainage. The posted outcome counts are 12 participants in the antibiotic arm and 11 in the placebo arm.

There is an inconsistency in how the design is represented: the registry labels the model as single-group while also listing randomized allocation, two treatment arms, and results for both arms. The record does not explain this discrepancy. The arm-level results and comparison are interpretable as a randomized comparison, but the model label should be kept in mind when reading the record.

The primary endpoint is a participant count for abscess resolution, with a 10-day timeframe and an intention-to-treat population designation. The description says resolution was assessed through parental report 7 - 10 days after the initial Emergency Center visit. The registry record does not report details of the randomization method, allocation concealment, treatment duration, adherence assessment, or original statistical plan. It also does not report the original sample-size justification.

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: Intention to treat

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: Intention to treat

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Abscess Resolution, measured over 10 days.

The primary endpoint counts participants whose abscess was considered resolved. The registry defines resolution as resolution of size, tenderness, and induration with erythema, assessed by parental report 7 - 10 days after the initial Emergency Center visit. The listed timeframe for the outcome is 10 days, and the analysis population is intention to treat.

A participant-level resolution outcome is clinically interpretable because it expresses the result as the number of people meeting the stated outcome definition, rather than as a change in a measurement scale. Comparing these counts between randomized arms can describe the observed difference in the proportion meeting the endpoint. In this record, the antibiotic arm had 11 of 12 participants with abscess resolution, and the placebo arm had 9 of 11.

The endpoint is intended to capture a short-term outcome after drainage, with the question being whether resolution was achieved by the stated follow-up. It is distinct from the secondary outcomes, which concern admission or changes in antibiotic treatment when resolution fails. The parental-report component is important to interpretation: the registry description does not indicate that the endpoint was based solely on an independently assessed physical examination.

The record does not report additional details about outcome adjudication, the handling of participants without an assessment, or whether the same assessment process was used in both arms. Those omissions limit how fully the endpoint’s measurement properties can be evaluated from the registry record alone.

7. Results Posted in the Registry

• Antibiotic Arm: 91.7% (11/12) versus 81.8% (9/11) on control; risk difference 9.8 percentage points (95% CI -17.8 to 37.5), risk ratio 1.12 (0.81–1.55); unadjusted two-proportion z-test p = 0.484.

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 Requiring New or Modified Antibiotics for Failure of Abscess to Resolve

• 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:
  • Antibiotic Arm: 8.3% (1/12) versus 18.2% (2/11) on control; risk difference -9.8 percentage points (95% CI -37.5 to 17.8), risk ratio 0.46 (0.05–4.38); unadjusted two-proportion z-test p = 0.484.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Antibiotic Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies two secondary outcomes: admission for failure of abscess resolution, and the need for new or modified antibiotics for failure of resolution. Two secondary outcomes are posted, alongside the primary resolution outcome. The registry record gives counts and comparisons for the antibiotic and placebo arms for the outcome concerning new or modified antibiotics, but does not report an analysis for the admission outcome. The secondary outcome listing and the results listing therefore do not provide a complete set of inferential results for every stated secondary question.

At a broad level, the secondary outcomes address possible consequences of unresolved abscesses and relate clinically to the primary question of resolution. They are not interchangeable with the primary endpoint: a change in antibiotic treatment or admission is a different event from resolution itself. Their results can provide additional context about the course of participants, but should not be treated as a substitute for the primary outcome comparison.

The secondary comparisons are unadjusted. General statistical explanation: examining multiple outcomes creates multiple opportunities for a result to appear unusual by chance. Without a reported multiplicity strategy, isolated unadjusted findings carry less evidential weight than a result that was prespecified and interpreted within a defined analysis plan. The registry record does not report such a strategy, nor does it report a hierarchy of outcomes or a correction for multiple testing.

The secondary findings should therefore be read as exploratory descriptive evidence rather than as independent confirmation of the primary comparison. Their interpretation is further limited by the small arm sizes and by the absence of a reported analysis for one of the listed secondary outcomes. The record does not provide details that would allow a more comprehensive assessment of these secondary questions.

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

• Number of Participants Requiring Admission for Failure of Abscess Resolution
• Number of Participants Requiring New or Modified Antibiotics for Failure of Abscess to Resolve

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant is counted according to whether the stated abscess-resolution outcome was met. General statistical explanation: when a binary outcome is compared between groups, the observed event proportions can be expressed as an absolute difference, a relative risk, or an odds ratio. Each describes the contrast on a different scale. The risk difference is an absolute contrast; relative risk compares the proportions as a ratio; and the odds ratio compares the odds of the outcome.

What does the risk difference describe?

The registry reports a risk difference of 0.099 for antibiotic treatment relative to placebo, with an interval from -0.178 to 0.375. In this comparison, a positive estimate points toward a higher proportion meeting the resolution endpoint in the antibiotic arm. A value of no difference is included within the reported interval. The estimate is based on the posted arm counts, and its interpretation should remain tied to that outcome and timeframe.

The arm proportions are also reported as p0 = 0.818 for placebo and p1 = 0.917 for antibiotic treatment. These are the proportions underlying the posted risk-difference comparison. The record’s counts are 9 of 11 and 11 of 12, respectively. Because the arm sizes are small, one participant’s outcome can have a substantial effect on the observed proportions. General statistical explanation: a small dataset often produces an unstable point estimate and a wide interval, because there is limited information about the range of outcomes that could occur in the underlying population.

Why are multiple effect scales shown?

The relative risk is reported as 1.12, with an interval from 0.808 to 1.553. The odds ratio is 2.444, with an interval from 0.190 to 31.53. These are not additional outcomes; they are alternative ways to express the primary comparison. Relative measures can be useful for describing proportional contrasts, while the risk difference directly describes an absolute contrast. Their intervals are wide, especially for the odds ratio, so the numerical point estimates should not be treated as precise summaries of the likely effect.

General statistical explanation: odds and probabilities are related but are not interchangeable. An odds ratio is not the same quantity as a ratio of probabilities. When an event is common, the numerical values of these measures can differ appreciably. The record presents all three measures, so the scale should be identified whenever the estimate is discussed.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.484. General statistical explanation: a p-value assesses how unusual data at least as incompatible with a specified null model would be if that model were true. It is not the probability that a treatment has no effect, and it does not indicate the probability that the observed estimate is correct. The p-value is unadjusted, and the registry record does not report a multiplicity procedure or a complete inferential analysis plan. It should therefore be read alongside the point estimate and interval, not as a stand-alone verdict.

The record lists no reported analyses in its analysis listing, while also presenting arm comparisons and unadjusted p-values. It does not clarify the origin or prespecification of these comparisons. No additional adjusted analysis is reported, and no covariate adjustment should be inferred.

What does intention to treat mean?

The primary outcome identifies its population as intention to treat. General statistical explanation: an intention-to-treat approach aims to analyze participants according to the groups to which they were randomized, preserving the original randomized comparison. However, the label alone does not explain how missing outcome information was handled, whether all randomized participants were included in the posted counts, or what rules were applied to withdrawals. The record does not report those details, so the analysis population label should not be expanded into assumptions about missing data.

The comparison is also limited by the low number of participants and the small number of outcome events that differ between the arms. General statistical explanation: with sparse binary data, estimates can be sensitive to individual observations, and uncertainty can remain large even when the point estimate appears notable. The posted interval makes that uncertainty visible. No alternative statistical method or adjusted model is described in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.099, with a confidence interval from -0.178 to 0.375. The interval covers both a possible negative difference and a possible positive difference. In plain terms, the posted data do not pin down a narrow range for the contrast between the treatment arms. The point estimate alone would conceal this uncertainty.

General statistical explanation: a confidence interval communicates the precision of an estimate by showing a range of values compatible with the data under the method used. A wider interval indicates less precision than a narrower one. An interval that includes no difference does not prove that the groups are identical; it indicates that the data do not distinguish the estimate from no difference at the interval’s stated level. The registry record does not state the confidence level used, so no level should be assumed from the record.

The relative-risk interval, from 0.808 to 1.553, also includes values on either side of no relative difference. The odds-ratio interval, from 0.190 to 31.53, is especially broad. These intervals reinforce that the comparison is imprecise across effect scales. The study’s posted arm counts—12 in the antibiotic arm and 11 in the placebo arm—are small, and the resulting estimates are sensitive to the outcomes of individual participants.

Precision is distinct from whether an estimate is favorable on a chosen scale. The risk-difference point estimate is positive, but its interval encompasses a broad range of possibilities. The p-value of 0.484 likewise does not replace the interval’s information about effect size and uncertainty. The registry record supports describing an observed contrast, but not a finely determined estimate of its magnitude.

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 participants across both arms. They are illustrative calculations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a design with 80% power under those planning assumptions and the effect size specified for that row. In plain language, power is the chance that a study designed under those assumptions would detect an effect of that size according to the selected statistical test. The 90% power column gives the corresponding per-arm planning number for a design with 90% power. These are prospective planning illustrations, not counts of participants who were enrolled in this trial.

The rows consider planning for 100%, 75%, and 50% of the observed effect. As the effect used for planning becomes smaller, the required number of participants per arm increases. For example, the registry’s figures for planning for 100% of the observed effect are 185 participants per arm for 80% power and 248 for 90% power; planning for 50% of the observed effect gives 857 and 1,147, respectively. The intermediate row gives 356 and 476. These are not observed power estimates for the completed trial.

General statistical explanation: smaller effects are harder to distinguish from random variation, so they typically require more information to detect under otherwise comparable assumptions. The figures depend on the stated planning choices, including the assumed effect, significance level, allocation, and approximation. They should not be treated as evidence that the completed trial was designed to meet these targets, because its original design assumptions are not reported.

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 = 0.818; treatment proportion p₁ = 0.917; average p̄ = 0.867.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4796 = 0.9400.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4745 = 0.3993.
4. n = (0.9400 + 0.3993)² / (0.0985)² = 184.9, rounded up to 185 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 <- 0.818181818181818                          # control proportion
p1 <- 0.916666666666667                          # 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(691600)
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 = 185 (80% power), 248 (90% power)
 75% of observed effect: n per arm = 356 (80% power), 476 (90% power)
 50% of observed effect: n per arm = 857 (80% power), 1,147 (90% power)
power.prop.test: 184.9 
Simulated power at n = 185 per arm: 0.812 (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 lists a primary outcome and two secondary outcomes, but it does not report a multiplicity plan. In particular, it does not describe whether one endpoint was designated as the sole confirmatory test, whether secondary outcomes were ordered in a hierarchy, or whether any adjustment was planned for examining multiple outcomes. The primary comparison is reported with an unadjusted p-value, and the secondary comparison is also unadjusted.

General statistical explanation: when several outcomes or comparisons are tested, the chance of obtaining at least one apparently unusual result by chance can increase. A prespecified strategy can clarify which comparisons carry confirmatory weight and how multiplicity is handled. Without that information, individual unadjusted p-values should be interpreted cautiously, especially for secondary outcomes. This does not invalidate the posted estimates, but it limits the strength of claims based on isolated significance tests.

The record identifies the primary analysis population as intention to treat. It does not report the number of participants with unavailable primary outcome data, reasons for missingness, imputation methods, or sensitivity analyses. It also does not explain how any participants without a parental report were handled. Consequently, the extent and impact of missing outcome data cannot be assessed from the registry record.

The registry provides no reported analyses in its analysis listing. It does not report the original statistical analysis plan, covariate adjustment, interim analyses, stopping rules, or details of the statistical test used to produce the posted p-value and intervals. These items are not presumed to have been absent from the conduct of the study; they are not reported in the registry record.

The distinction between information not reported and procedures not used is important. The registry allows a reader to describe the posted counts and comparisons, but it does not support a detailed audit of prespecification, missing-data handling, or the complete inferential strategy. These gaps affect how strongly the results can be interpreted, particularly for secondary comparisons and multiplicity-sensitive conclusions.

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 0% reporting threshold.

The posted serious adverse event figures are 0 affected participants among 12 at risk in the antibiotic arm and 0 among 11 at risk in the placebo arm. The registry also reports 0 deaths in each arm. No serious adverse event terms are listed among the leading serious-event terms.

These figures describe what was recorded in the registry for the participants at risk in each group. They do not establish that no adverse events of any kind occurred: the record separates serious adverse events from other adverse events, and it reports 0 affected participants in the other-adverse-event category in both arms as well. The small numbers of participants mean that these counts provide limited information about uncommon events.

General statistical explanation: observing no events in a small group does not show that the underlying risk is zero. It means that no participants in that group were recorded as having the specified event during the reporting period or under the reporting definitions used. The registry record does not give further detail about event definitions, duration of safety follow-up, or the method of event collection.

The safety counts should therefore be read descriptively and within the limits of the small enrolled groups. They do not establish comparative safety with precision, and they do not support conclusions about events not captured in the registry record.

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

The results describe a small randomized comparison of oral trimethoprim/sulfamethoxazole and placebo after incision and drainage for pediatric abscesses less than 5 cm. The primary outcome was abscess resolution at 10 days, and the observed counts were 11 of 12 participants in the antibiotic arm and 9 of 11 in the placebo arm. The posted risk-difference estimate is 0.099, with an interval from -0.178 to 0.375.

Those data show a point estimate in the direction of more participants meeting the resolution outcome in the antibiotic arm, but the estimate is imprecise. Its interval includes differences in either direction, and the unadjusted p-value is 0.484. The evidence does not establish a precise treatment contrast. A non-significant p-value should not be translated into proof that the groups are equivalent, just as the positive point estimate should not be treated as proof of a benefit.

The record also does not provide the original sample-size assumptions, a detailed statistical analysis plan, or information about missing outcome data. It labels the primary analysis population as intention to treat but does not explain how that was implemented. The model is labeled single-group despite the randomized allocation and two reported arms. Such limitations leave uncertainty about aspects of study conduct and analysis beyond the uncertainty visible in the effect interval.

These results do not determine what treatment an individual child should receive, and they are not medical advice. They apply to the population and outcome described in the registry record and should not automatically be extended to other abscess sizes, populations, treatments, or follow-up periods. The registry reports a completed Phase 3 study, but the sample and the information available in the record are limited for making precise claims.

The appropriate statistical reading is restrained: the posted data give an observed comparison, but leave substantial uncertainty about the size and direction of the underlying difference. The record does not support a definitive conclusion about equivalence or a precisely quantified effect.

17. Why This Trial Matters Statistically

This trial illustrates the difference between a point estimate and the information available to support it. The primary risk-difference estimate is positive, but its interval ranges from -0.178 to 0.375. Considering only the direction of the point estimate would miss the broad uncertainty around it. For clinical research readers, the interval is an essential part of the result, not an optional supplement to the p-value.

The arm counts also show why small studies require cautious interpretation. The comparison includes 12 participants in the antibiotic arm and 11 in the placebo arm. With such limited counts, a small number of participant outcomes can materially affect the observed proportions and effect estimates. This helps explain why the registry’s intervals are broad and why the results do not tightly determine the treatment contrast.

The registry record also provides an instructive contrast between retrospective planning illustrations and the trial’s original design. The sample-size calculations are based on fractions of the observed effect and stated planning assumptions, but the original sample-size justification is not reported. These planning figures can help readers understand how assumptions about a target effect relate to required enrollment; they cannot establish that the trial was originally planned around those assumptions or reveal its observed power.

Finally, the record highlights the importance of transparent analysis reporting. It names an intention-to-treat population but does not explain missing-data handling, multiplicity, or the complete inferential plan. In addition, the single-group model label sits alongside randomized allocation and two arms. Identifying these uncertainties is part of sound statistical interpretation: the posted findings can be described, while unresolved record details remain explicit.

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.

The primary limitation for interpreting the numerical comparison is the small number of participants: 12 in the antibiotic arm and 11 in the placebo arm. The primary outcome counts are correspondingly limited, and the posted confidence interval is broad. The results cannot provide a precise estimate of the difference in resolution between groups.

The endpoint includes parental report 7 - 10 days after the initial Emergency Center visit. The record does not report further details about assessment procedures, outcome adjudication, or how missing reports were handled. Although the primary population is labeled intention to treat, it is not clear from the registry record whether all randomized participants had outcome data or how incomplete data were incorporated.

The registry describes randomized allocation and quadruple masking, but the model is labeled single-group despite the two listed arms and their comparative results. The record does not explain this inconsistency. It also does not report the randomization method, allocation concealment, treatment duration, adherence information, or the study’s original sample-size justification.

The analysis reporting is limited. The record lists no reported analyses in its analysis listing, while presenting unadjusted comparisons. It does not report the statistical analysis plan, covariate adjustment, interim analyses, or multiplicity handling. One listed secondary outcome, admission for failure of resolution, does not have a posted comparison in the results described in the record. The available secondary results therefore do not answer all secondary questions listed.

Finally, the safety counts are based on the small groups and do not establish the absence of uncommon events. These limitations are specific to the information and results recorded for this trial and should be considered alongside, rather than substituted for, the uncertainty expressed by the primary effect interval.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Management of Skin and Soft Tissue Abscesses in Pediatric Patients After Incision and Drainage — NCT00691600.
• Registry record last updated 2020-07-01; status last verified 2020-06.
• Results first posted 2020-06-23.
• 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 record describes a completed Phase 3 randomized study sponsored by Baylor College of Medicine, comparing oral trimethoprim/sulfamethoxazole with placebo after incision and drainage of pediatric abscesses less than 5 cm. Enrollment was 23, and the record identifies quadruple masking. The primary outcome was participant-level abscess resolution at 10 days in an intention-to-treat population.

Resolution was described as resolution of size, tenderness, and induration with erythema, based on parental report 7 - 10 days after the initial Emergency Center visit. The posted counts were 11 of 12 participants in the antibiotic arm and 9 of 11 in the placebo arm. The risk-difference estimate was 0.099, with an interval from -0.178 to 0.375 and an unadjusted p-value of 0.484.

The estimate is imprecise, and the interval includes differences in both directions. The registry does not report the original sample-size justification, a complete statistical analysis plan, or details of missing-data and multiplicity handling. The results are best read as a limited comparison with substantial uncertainty rather than as a precise determination of the treatment contrast.