Evaluation of a Staphylococcus Eradication Protocol for Patients Who Present to the ED With Cutaneous Abscess: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of a Staphylococcus Eradication Protocol for Patients Who Present to the ED With Cutaneous Abscess (NCT01537783), a randomized phase 4 study. The primary outcome is Recurrence of Cutaneous Abscess.

2. Clinical Question

The question is clinically specific: it concerns recurrence after an emergency-department visit for an abscess, rather than initial treatment success or a general measure of infection. The posted endpoint records a participant’s description of another abscess since that visit. The comparison therefore depends on reported recurrence, not on a registry description of clinical examination or independent confirmation of each event.

The intervention was added to routine care, while standard care could vary according to clinician judgment. This matters when interpreting the comparison: it is between assignment to a decontamination protocol plus usual care and usual care alone, not between two fully specified wound-care regimens. The registry record does not report further details about eligibility criteria or the intended analysis population.

3. Trial Design

The registry describes a randomized, parallel-group, unmasked trial of a Staphylococcus eradication protocol for patients presenting to the emergency department with cutaneous abscess. It lists the study as Phase 4 and completed. Tufts Medical Center is named as sponsor. The registry reports enrollment of 50, a start date of 2011-09, and primary completion in 2013-09.

Participants were assigned to an intervention group or standard care. In the intervention group, chlorhexidine scrubs were used once a day for 5 days and mupirocin was applied to both nostrils twice a day for 5 days. The registry says both treatments began 7 days after enrollment, or when the abscess had healed fully if it had not healed by day 7. In the standard-of-care group, routine abscess care could include topical or oral antibiotics at the treating clinician’s discretion.

The study summary describes follow-up calls at 7 days, 14 days for the treatment arm, 3 months, and 6 months to ask about recurrence. The primary endpoint is reported at 6 months. The posted primary-outcome counts are 5 participants in the intervention group, with an outcome denominator of 14, and 7 in standard care, with an outcome denominator of 23. These outcome denominators are the ones reported with the endpoint; the registry record does not explain their relationship to the enrollment figure.

The registry identifies randomization but does not report the sequence-generation method, allocation concealment, or blinding procedures. Masking is listed as none. The original sample-size justification, planned analysis methods, and any protocol amendments are not reported in the registry record. Thus, the design can be described from the recorded assignment and treatment details, but its unreported operational features should not be inferred.

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 Recurrence of Cutaneous Abscess, measured over 6 months.

The primary endpoint is recurrence of cutaneous abscess at 6 months, measured as a count of participants. The registry defines an event as a participant’s description that they had another abscess since the index emergency-department visit. The posted results list 5 participants with recurrence among 14 in the intervention group and 7 among 23 in standard care.

A recurrence endpoint addresses whether another abscess was reported after the initial emergency-department visit. Recording the number of participants with an event gives a binary outcome for each participant: a recurrence was reported or it was not recorded as reported. This form of outcome can support comparisons of event risk between randomized groups. That is a general statistical property of binary endpoints, not evidence about the quality of event ascertainment in this trial.

The registry does not describe independent confirmation, medical-record review, or a standard diagnostic definition beyond the participant’s description. Consequently, the endpoint represents reported recurrence rather than a registry-documented, independently adjudicated event. The record also does not explain how participants with no follow-up response were classified or handled.

The 6-month time point gives the outcome a defined follow-up horizon. Recurrences outside that horizon are not represented by this primary endpoint, and the posted result does not summarize time to recurrence. The record lists no secondary outcomes. These features make the endpoint focused, while leaving important details about ascertainment and missing follow-up unreported.

7. Results Posted in the Registry

• Intervention Group: 35.7% (5/14) versus 30.4% (7/23) on control; risk difference 5.3 percentage points (95% CI -26.1 to 36.6), risk ratio 1.17 (0.46–2.99); unadjusted two-proportion z-test p = 0.739.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: recurrence was either reported or not reported for the endpoint. For binary outcomes, a group risk is the proportion of participants in that group who experienced the event. The registry reports group proportions of 0.357 for the intervention group and 0.304 for standard care, based on the posted event counts and denominators. Comparing such proportions is a direct way to describe how often the endpoint occurred in each group.

What does the risk difference express?

The risk difference expresses the absolute contrast between the two group risks. The posted estimate is 0.053. Its sign reflects the direction of the contrast as reported, with a positive value indicating a higher observed risk in the intervention group. An absolute measure is useful because it describes the gap between group risks on the same scale as those risks. The estimate is not, by itself, proof of a causal effect; interpretation also depends on uncertainty, outcome ascertainment, and how participants with missing follow-up were handled.

How do relative measures differ?

The risk ratio compares one group’s risk with the other group’s risk as a relative quantity. The posted estimate is 1.173. A value at the point representing equal risks is the reference for no relative difference; values on either side indicate opposite directions. The odds ratio compares event odds rather than risks, and its posted estimate is 1.27. Odds and risks are different quantities, so an odds ratio should not be read as though it were a risk difference or a risk ratio. Here, the confidence intervals for both relative measures are broad and include values indicating effects in either direction.

What does a confidence interval contribute?

A confidence interval conveys the uncertainty around an estimate under the statistical method used. In repeated use of a method under its assumptions, intervals constructed in this way have a defined long-run coverage property. For a single trial, the interval does not assign a probability to the true effect being inside its particular bounds. It provides a range of effect values compatible with the data and method, and helps show whether the estimate is precise enough to distinguish among clinically meaningful possibilities. The risk-difference interval extends from -0.261 to 0.366, which is wide and spans the no-difference value.

What does the p-value say?

The unadjusted p-value is 0.739. A p-value describes how unusual data at least as incompatible with a specified no-difference model would be under that model and the test assumptions. It is not the probability that the no-difference model is true, and it does not measure the size or clinical importance of an effect. The record does not state which exact test or model generated this value, so details of its calculation are not reported in the registry record.

Why do the estimates remain uncertain?

Precision is affected by the amount of information in the outcome data and by the variability inherent in a binary endpoint. When events and denominators are limited, a small change in observed outcomes can have a noticeable influence on an estimated contrast. Randomization helps protect the comparison from systematic assignment differences, but it does not remove sampling variability. Broad intervals are therefore important to emphasize alongside the point estimates.

Risk differences, risk ratios, odds ratios, confidence intervals, and p-values answer related but distinct questions. The difference describes an absolute contrast, the ratios describe relative contrasts, the interval describes uncertainty, and the p-value describes compatibility with a specified null model under a test. None should be interpreted in isolation. The registry record does not report a detailed statistical analysis plan, adjustment variables, or the handling of missing outcomes; those methods cannot be assumed from the posted summary statistics.

10. Confidence Intervals and Precision

The principal precision message is that the estimated risk difference is uncertain. Its posted value is 0.053, with a confidence interval from -0.261 to 0.366. This interval spans the no-difference value and includes estimates in either direction. It is wide relative to the point estimate, so the data do not determine the size or direction of the underlying contrast precisely.

The relative estimates show a similar limitation. The risk ratio is 1.173, with a confidence interval from 0.460 to 2.991. The odds ratio is 1.27, with a confidence interval from 0.310 to 5.194. Each interval includes values corresponding to effects in opposing directions. The point estimates therefore should not be read as settled evidence that recurrence was higher or lower under either assignment.

A confidence interval is not a range of values that the true effect has a stated probability of occupying. It is an uncertainty summary generated by a statistical procedure. In practical reading, a broad interval means that the observed data are compatible with a range of possible effects, rather than supporting a sharply defined estimate. The interval’s width matters even when a point estimate appears easy to summarize.

The posted outcome counts are 5 among 14 in the intervention group and 7 among 23 in standard care. The limited outcome information contributes to uncertainty, although the registry record does not provide a formal decomposition of the reasons for the interval width. Missing-data handling and details of the analysis method are not reported in the registry record. These omissions further 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 sample-size figures are planning illustrations based on the observed effect, not a record of the trial’s original design calculation. The listed figures are participants per arm, not total events. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is stated as a fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 1,246 participants per arm for 80% power and 1,667 participants per arm for 90% power. For planning at 75% of the observed effect, they are 2,193 participants per arm for 80% power and 2,935 participants per arm for 90% power. For planning at 50% of the observed effect, they are 4,881 participants per arm for 80% power and 6,534 participants per arm for 90% power.

The 80% power column represents the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one and the model assumptions held. The 90% power column gives the corresponding planning target for a greater chance of detection. These are design probabilities, not guarantees of a statistically significant result.

The table and curve express the general planning relationship: smaller effects require more participants to detect, because a smaller contrast is harder to distinguish from random variation. The trial’s original sample-size assumptions and justification are not reported in the registry record. These planning figures are not observed power; observed power is not an interpretation of the trial’s result.

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 = 0.304; treatment proportion p₁ = 0.357; average p̄ = 0.331.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6654 = 1.3041.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6643 = 0.5591.
4. n = (1.3041 + 0.5591)² / (0.0528)² = 1,245.4, rounded up to 1,246 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 <- 0.304347826086957                          # control proportion
p1 <- 0.357142857142857                          # 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(1537783)
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 = 1,246 (80% power), 1,667 (90% power)
 75% of observed effect: n per arm = 2,193 (80% power), 2,935 (90% power)
 50% of observed effect: n per arm = 4,881 (80% power), 6,534 (90% power)
power.prop.test: 1245.4 
Simulated power at n = 1,246 per arm: 0.801 (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 one primary outcome measure, recurrence of cutaneous abscess at 6 months, and no secondary outcomes. It records no posted analyses. The registry record does not report a full analysis plan, including whether additional outcomes or subgroup analyses were planned outside the posted record.

Multiplicity arises when several outcomes, time points, subgroups, or statistical tests are examined. Testing many hypotheses can increase the chance that at least one appears unusual by chance. Statistical plans may address this through a hierarchy of outcomes, adjustment procedures, or other approaches. Whether any such procedures were planned or used for this trial is not reported in the registry record. The unadjusted p-value should therefore be understood as the posted unadjusted comparison, not as evidence that multiplicity was addressed.

The registry describes follow-up calls at 7 days, 14 days for the treatment arm, 3 months, and 6 months. It does not report how all follow-up time points were analyzed or whether any were intended as additional efficacy outcomes. The primary result discussed is the 6-month recurrence outcome. No inference about unposted time-point analyses should be made.

The outcome denominators are 14 for the intervention group and 23 for standard care. The registry record does not explain why those denominators differ from each other or how they relate to the enrollment figure. It does not report the amount or pattern of missing outcome data, the number of participants who could not be reached, or the rules used to classify missing responses. It is therefore not possible to assess whether missingness could have affected the observed comparison.

The analysis population is not specified in the primary outcome record. The registry does not say whether the comparison used all randomized participants, participants with available follow-up, or another defined group. It also does not report whether participants were analyzed according to assigned group or according to treatment received. These are distinct analysis choices, and none should be inferred. The available result can be described as posted, while questions about missingness, analysis population, and multiplicity remain unresolved by the registry record.

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.

For serious adverse events, the registry lists 25 participants at risk in the intervention group and 25 in standard care, with 0 serious adverse events in each group. It also lists 25 participants at risk in each group for other adverse events, with 0 other adverse events in each group. Death counts are not reported in the registry record.

These entries describe the adverse-event fields recorded in the registry; they do not establish that no adverse experiences occurred outside the definitions, observation procedures, or reporting scope used for those fields. The record does not describe the collection method, observation period, event definitions, or the completeness of safety follow-up. It also lists no serious adverse-event terms.

The adverse-event denominators are the registry’s reported at-risk counts. They differ from the primary-outcome denominators, and the registry record does not explain the relationship between these sets of counts. Safety results should therefore be read separately from the recurrence endpoint and without assuming that their populations or follow-up procedures were identical.

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

The posted data show reported recurrence in both groups: 5 participants among 14 in the intervention group and 7 among 23 in standard care. The estimated risk difference is 0.053, with a confidence interval from -0.261 to 0.366, and the unadjusted p-value is 0.739. The confidence interval is broad and includes no difference, while the point estimate is in the direction of higher observed recurrence in the intervention group.

This result does not establish that the decontamination protocol reduced recurrence, nor does it establish that the protocol increased recurrence. The estimate is imprecise, and the data are compatible with different underlying effects. A non-small p-value is not evidence that the groups are equivalent; demonstrating equivalence would require an appropriate design and prespecified criteria, which are not reported in the registry record.

The outcome was based on participants’ descriptions of another abscess after their index emergency-department visit. The registry record does not describe independent event confirmation or how missing follow-up was handled. The posted comparison should therefore be interpreted as a comparison of reported events in the outcome data, not as a definitive account of all recurrences or of a biologically verified outcome.

Randomization is an important feature of the design because it is intended to make assigned groups comparable on average. It does not ensure that the recorded outcome is complete, eliminate chance variation, or compensate for uncertainty in the estimate. In addition, the comparator allowed usual care at the treating clinician’s discretion, so the contrast was not between the protocol and a single fixed co-intervention regimen.

The result is most appropriately read as an uncertain estimate from a completed randomized trial with a specific 6-month self-reported recurrence endpoint. The registry record does not provide secondary outcomes, detailed analysis methods, missing-data procedures, or an original sample-size justification. Those gaps constrain how far the posted comparison can be interpreted. No conclusion about individual care follows from this statistical summary.

16. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison and a clear endpoint do not, by themselves, guarantee a precise answer. The study addresses a focused clinical question: whether adding a decontamination protocol to routine care is associated with a different frequency of reported abscess recurrence by 6 months. The posted outcome is interpretable as a participant-level binary event, and the registry provides both group counts and comparative estimates.

The precision is the central statistical issue. The risk-difference estimate is 0.053, but its confidence interval extends from -0.261 to 0.366. That range is broad and spans possible effects in either direction. The risk-ratio and odds-ratio intervals are also broad. A simple emphasis on the point estimate or p-value would miss the extent of uncertainty in the data.

The endpoint also shows how measurement choices shape conclusions. A participant’s report of another abscess captures recurrence from the participant’s perspective, but the registry does not report independent verification or details of follow-up completion. Understanding those features is part of evaluating what an estimate represents, not merely a technical footnote.

The registry’s missing analysis details matter as well. It does not report a detailed statistical plan, analysis population, missing-data method, or original sample-size justification. These omissions prevent a full assessment of how design choices and incomplete follow-up may have influenced the posted result. They do not invalidate the reported counts, but they define the limits of what can be inferred from the registry record.

For biostatistical interpretation, the trial is a useful example of keeping the estimate, interval, endpoint definition, and reporting context together. The observed comparison is informative as a description of these posted data, while remaining insufficiently precise to settle the size or direction of a broader effect.

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 limitations specific to this trial constrain interpretation. The primary endpoint is based on a participant’s description of another abscess. The registry record does not report independent confirmation, a more detailed diagnostic definition, or adjudication procedures. The result therefore concerns reported recurrence as defined in the record.

The outcome denominators are 14 for the intervention group and 23 for standard care. The registry does not explain the difference between these denominators or their relationship to the enrollment figure of 50. It also does not report the number or pattern of missing follow-up responses, how nonresponse was handled, or the analysis population. The potential influence of incomplete outcome data cannot be assessed from the record.

The standard-care arm allowed topical or oral antibiotics at the treating clinician’s discretion. This makes the comparator a usual-care strategy rather than a uniform regimen. The registry does not provide further information about the care received in that group or how variation in co-interventions was considered analytically.

The trial was unmasked, and the outcome depended on participant report. The registry does not describe how knowledge of assignment was addressed in outcome ascertainment. This does not establish that reporting was biased, but it leaves that possibility unassessed in the available record.

The registry does not report the original sample-size justification, a detailed statistical analysis plan, the exact test underlying the unadjusted p-value, or any multiplicity procedure. It lists no secondary outcomes and no posted analyses. These reporting gaps limit appraisal of prespecification and robustness. Finally, the confidence intervals are broad, so the posted estimates leave substantial uncertainty about the magnitude and direction of the underlying comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Evaluation of a Staphylococcus Eradication Protocol for Patients Who Present to the ED With Cutaneous Abscess — NCT01537783.
• Registry record last updated 2017-04-13; status last verified 2017-03.
• Results first posted 2017-03-13.
• 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 registry record describes a completed, randomized, parallel-group, unmasked Phase 4 trial sponsored by Tufts Medical Center. The study concerned patients presenting to the emergency department with cutaneous abscess. Registry enrollment is 50; the start date is 2011-09 and primary completion is 2013-09.

The intervention combined routine abscess care with chlorhexidine scrubs and mupirocin nasal ointment. The comparator was standard care, which could include topical or oral antibiotics at clinician discretion. The primary endpoint was participant-reported recurrence of cutaneous abscess at 6 months.

The posted outcome counts were 5 among 14 in the intervention group and 7 among 23 in standard care. The risk difference was 0.053, with a confidence interval from -0.261 to 0.366; the unadjusted p-value was 0.739. The interval is broad and includes no difference. The registry record does not report secondary outcomes, posted analyses, an original sample-size justification, missing-data procedures, or a detailed analysis plan.