Study of New Antibiotic Regimen for the Treatment of Uncomplicated Cellulitis in Emergency Department Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of New Antibiotic Regimen for the Treatment of Uncomplicated Cellulitis in Emergency Department Patients (NCT00676130), a randomized na study. The primary outcome is Relative Efficacy.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with triple masking. It enrolled 153 participants and is marked completed in the registry. The record lists the study start as 2007-05 and primary completion as 2012-05. The phase is listed as NA. The specific people or roles covered by triple masking are not reported in the registry record.

The two groups received a common standard treatment, cephalexin, with either trimethoprim-sulfamethoxazole or placebo added. The registry labels these arms as standard therapy plus anti-CA-MRSA treatment and standard therapy, respectively. This design targets the additional effect associated with the study drug over the shared standard treatment, rather than comparing cephalexin with no treatment.

The registry summary describes an adult emergency-department population with uncomplicated cellulitis. It reports that four subjects were randomized in error and did not receive study drug, one received two doses before being found ineligible, one was lost to follow-up, and one withdrew voluntarily in the first few days after enrollment. It then states that 146 subjects remained for an intent-to-treat anal...; the description is truncated, so the full analysis-population definition is not reported in the registry record.

The primary outcome was treatment success, assessed at 12 +/- 2 days and confirmed at 30 +/- 2 days. Progression to abscess was the posted secondary outcome. The registry does not report the original design assumptions, the detailed randomization procedure, or which individuals were masked.

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: Each subject was assigned randomly to a treatment group by the institutions' research pharmacies. The research pharmacies had no knowledge of subjects' clinical characteristics. Treating (non-research) clinicians, research clinicians, coordinators, and subjects had no knowledge of the randomization sequence.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Of the 153 randomized subjects, 4 were randomized in error and did not receive study drug, 1 received two doses before it was discovered that he was ineligible, 1 was lost to follow up, and 1 withdrew voluntarily in the first few days after enrollment. This left 146 subjects for intent-to-treat 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 Relative Efficacy, measured over 12 +/- 2 days; 30 +/- 2 days.

The primary endpoint, titled Relative Efficacy, counts participants whose treatment was classified as successful. Physician examination at 12 +/- 2 days was the main assessment. The registry defines non-success as subsequent hospitalization, a change in antibiotics, surgical or needle drainage of an abscess, or recurrence of infection within 30 days. Cure required resolution of all symptoms other than mild residual erythema or edema. The cure determination was confirmed by telephone interview and medical record review at 30 +/- 2 days.

A binary success outcome is useful because it combines clinically relevant events into a clear classification: each participant either meets the stated success definition or does not. Comparing the proportions classified as successful gives a direct summary of how often the endpoint occurred in each randomized group. The definition also makes clear that success is not simply absence of symptoms at one visit; subsequent events within the specified follow-up can change the classification.

Endpoint interpretation depends on the operational definition and follow-up as well as the observed counts. The registry identifies the assessment timeframes and the events counted as non-success, but does not report further details about adjudication procedures or how missing endpoint assessments were handled.

7. Results Posted in the Registry

• Trimethoprim-sulfamethoxazole: 84.9% (62/73) versus 82.2% (60/73) on control; risk difference 2.7 percentage points (95% CI -9.3 to 14.8), risk ratio 1.03 (0.89–1.19); unadjusted two-proportion z-test p = 0.655.

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.

Progression to Abscess

• 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:
  • Trimethoprim-sulfamethoxazole: 6.8% (5/73) versus 6.8% (5/73) on control; risk difference 0.0 percentage points (95% CI -8.2 to 8.2), risk ratio 1.00 (0.30–3.31); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trimethoprim-sulfamethoxazole and the control. The interval gives the range of effects that remain compatible with the data.

Progression to abscess is the one secondary outcome posted. The overall pattern does not add a clear directional separation between the groups, and its uncertainty means it offers limited additional support for interpreting the primary result. The secondary endpoint concerns a related clinical event, but it is not the same as the primary composite definition of treatment success.

Secondary outcomes can help describe aspects of the trial that are not fully captured by the primary endpoint. They should generally carry less weight than the primary outcome when they are not the main basis for the study question. Their interpretation is also affected by multiplicity: assessing several outcomes increases the opportunity for chance findings, especially when results are treated as confirmatory without adjustment or a prespecified hierarchy.

The registry lists two outcome measures and two analyses, but does not report a multiplicity adjustment or a hierarchy for interpreting outcomes. The secondary result should therefore be viewed as supplementary rather than as an independent confirmation of the primary result. The small number of posted secondary outcomes also limits how much can be inferred about other potential clinical outcomes.

In general, concordance across carefully prespecified outcomes can strengthen a coherent interpretation, while differences may reflect the distinct events being measured or random variation. Here, the available secondary information does not resolve the discrepancy between the sponsor's primary analysis and the unadjusted re-calculation. Nor does it substitute for the incomplete information on missing data and analysis populations.

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

• Progression to Abscess

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary: each participant is classified as having successful treatment or not according to the registry definition. For this kind of endpoint, the observed proportion in each group is the number with the event divided by the number assessed in that group. The posted counts are 62 of 73 for trimethoprim-sulfamethoxazole and 60 of 73 for placebo. The group proportions are also given as 0.849 and 0.822 in the re-calculation.

A risk difference subtracts the event proportion in the comparison group from the event proportion in the treatment group. It expresses the contrast on the absolute scale: a value of zero corresponds to equal proportions, a positive value indicates a higher success proportion in the trimethoprim-sulfamethoxazole group, and a negative value indicates a lower one. The re-calculated risk difference is 0.027. The registry's reported risk difference is 2.7. The differing numerical formats reflect the values as recorded in the respective analyses; the registry record does not explain the discrepancy in the analysis results.

The re-calculation also gives a risk ratio of 1.033, with a confidence interval from 0.895 to 1.193, and an odds ratio of 1.221, with a confidence interval from 0.508 to 2.938. These are alternative ways to describe a binary-outcome contrast. A risk ratio compares the proportions directly; an odds ratio compares the odds of the outcome. Neither measure should be interpreted without its scale and uncertainty. In particular, a ratio centered around one represents no relative difference, while one on either side represents a difference in opposite directions.

A confidence interval describes the range of effect values that are reasonably compatible with the data under the method used. It is not a guarantee that the true value lies within the interval, and it does not show the probability that a specific treatment effect is true. A wide interval signals that the estimate is imprecise. When an interval includes the null value for its measure, the data do not sharply distinguish that null from values on either side, although a confidence interval should not be treated as the only evidence relevant to interpretation.

The registry lists a chi-squared method for the sponsor's primary analysis and labels its parameter Risk Difference (RD). A chi-squared test is a general method for evaluating whether categorical outcome distributions differ between groups. The posted sponsor p-value is <0.05, while the simple unadjusted re-calculation gives p = 0.655. These are discordant. The sponsor's own analysis takes precedence, but the reason for the discrepancy is not reported in the registry record. Details sufficient to reproduce the sponsor's calculation are not reported either.

The unadjusted re-calculation uses the posted group counts and sample sizes to estimate the between-group contrast without adjustment for other variables. It is not a substitute for a prespecified sponsor analysis, and it does not explain the sponsor's result. A difference between analyses can arise for multiple reasons in general, including different analysis populations, outcome handling, or statistical methods; which, if any, applies to this trial is not reported in the registry record.

Randomization is intended to support a fair comparison by allocating participants to groups without basing assignment on their observed characteristics. Masking can help limit the influence of knowledge about assignment on care, assessment, or reporting. The record identifies randomized allocation and triple masking, but does not give enough detail to assess the randomization procedure or determine which parties were masked.

For binary outcomes, the precision of a risk difference depends in part on the number of participants and the event proportions in both groups. General statistical principle: fewer observations or less balanced information about events usually means greater uncertainty. The posted confidence intervals reflect that uncertainty for their respective calculations; they are not evidence that all possible sources of bias or missing data have been addressed.

Interpretation also requires attention to the endpoint definition, analysis population, and handling of unavailable outcome information. The registry's population description is truncated after referring to an intent-to-treat analysis, and its missing-data methods are not reported in the registry record. Thus the posted analysis cannot be fully reconstructed from the record alone.

11. Confidence Intervals and Precision

The re-calculated primary risk difference is 0.027, with a 95% confidence interval from -0.093 to 0.148. The interval includes zero, so the re-calculation does not locate the contrast precisely on one side of no difference. It also allows values that would represent a difference in either direction. The width of the interval indicates substantial uncertainty about the size and direction of the effect.

The sponsor's reported 95% confidence interval runs from -9.3 to 15, accompanying a reported risk difference of 2.7. That interval also crosses zero. Its p-value is reported as <0.05, unlike the re-calculated p-value of 0.655. The registry record does not reconcile the inferential mismatch. Because the discrepancy flag is true, the sponsor's own analysis takes precedence, while the separate re-calculation remains a transparent, unadjusted calculation from the posted summary counts.

In general, a confidence interval is more informative than a point estimate alone because it conveys a range of effect sizes compatible with the data under the analysis. It does not measure the probability that the treatment has a particular effect, nor does it account automatically for bias, missing outcomes, or unreported analysis choices. Here, the range of plausible values is broad relative to the point estimate, so precision is limited.

The registry does not report a sample-size justification or the original design assumptions. Consequently, the observed interval should be read as evidence about uncertainty in the posted results, not as proof that the trial was designed to detect a particular effect with a particular precision.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design assumptions. The record specifies 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 the stated fraction of the observed effect. The registry's original sample-size assumptions are not reported in the registry record.

The figures are participants per arm for this binary outcome. The 80% power column gives the planned number of participants in each arm for a calculation with an 80% chance of detecting the selected effect under the stated planning assumptions, if that effect is the true one. The 90% power column gives the corresponding per-arm planning number for 90% power. These are design calculations; they are not descriptions of how many participants were actually enrolled in this trial.

The listed scenarios are planning for 100% of the observed effect, planning for 75% of the observed effect, and planning for 50% of the observed effect. As the effect being targeted becomes smaller, more participants are needed to distinguish it from random variation under the same assumptions. The figures rise across those scenarios for that reason.

These calculations are illustrations rather than a retrospective score of the trial. They do not show the probability that the trial's result is true, and they are not observed power. Their usefulness depends on the observed effect being a reasonable planning value and on the stated assumptions being suitable for a future design. The record does not report whether those assumptions match the trial's original planning.

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 = 0.822; treatment proportion p₁ = 0.849; average p̄ = 0.836.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5241 = 1.0273.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5238 = 0.4408.
4. n = (1.0273 + 0.4408)² / (0.0274)² = 2,871.5, rounded up to 2,872 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 <- 0.821917808219178                          # control proportion
p1 <- 0.849315068493151                          # 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(676130)
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 = 2,872 (80% power), 3,844 (90% power)
 75% of observed effect: n per arm = 5,191 (80% power), 6,949 (90% power)
 50% of observed effect: n per arm = 11,871 (80% power), 15,891 (90% power)
power.prop.test: 2871.5 
Simulated power at n = 2,872 per arm: 0.796 (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. Analyses Reported by the Sponsor

The registry reports a chi-squared analysis with a risk difference of 2.7, a 95% confidence interval from -9.3 to 15, and p <0.05. A separate unadjusted re-calculation from the posted counts gives a risk difference of 0.027, a 95% confidence interval from -0.093 to 0.148, and p = 0.655. The values and inferential summaries do not agree.

Because the discrepancy flag is true, the sponsor's own analysis takes precedence over the simple re-calculation. This does not make the difference between them unimportant: the record does not explain why they diverge or give enough analysis detail to reproduce the sponsor's result. The re-calculation should be understood as an unadjusted check based on the posted summary statistics, not as a correction to the sponsor's analysis.

The sponsor's reported interval includes zero even though its p-value is reported as <0.05. Those reported values are themselves difficult to reconcile using the usual relationship between a two-sided 95% confidence interval and a corresponding test. The registry record does not report whether a different convention or analysis detail accounts for that pattern. The prudent reading is to retain the sponsor's result as the official posted analysis, clearly note the inconsistency, and avoid presenting the re-calculation as if it resolves the uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists the primary outcome and one secondary outcome, and records two analyses. Whether the investigators planned a hierarchy among outcomes, adjusted for multiple comparisons, or used a particular approach to control the chance of false-positive findings is not reported in the registry record. This matters because testing or interpreting multiple outcomes can increase the chance that at least one appears noteworthy by chance. The extent of that concern depends on the analysis plan and the role assigned to each outcome; those details are unavailable.

The population account states that 153 subjects were randomized, then describes four randomized in error who did not receive study drug, one participant who received two doses before being found ineligible, one lost to follow-up, and one voluntary withdrawal in the first few days. It says 146 subjects remained for an intent-to-treat anal..., but the registry text is truncated. The full definition of that analysis population is not reported in the registry record.

How missing primary outcome data were handled is not reported in the registry record. The record also does not state whether the analysis followed randomized assignment for all participants, whether any participants were excluded from the reported endpoint analysis, or what assumptions were made about unavailable outcomes. These details can affect an estimate, particularly when outcome availability or exclusions differ between groups.

It is also not reported whether there were interim analyses, whether the analysis was adjusted for baseline characteristics, or what other elements were specified in the statistical analysis plan. No assumptions about those procedures can be made from the posted results. The reporting discrepancy between the sponsor analysis and the unadjusted re-calculation further limits independent reconstruction, and the registry does not identify its cause.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: clostridium difficile colitis (1.4%).

The serious adverse event figures list zero serious events among 73 participants in the trimethoprim-sulfamethoxazole group and one among 73 in the placebo group. The registry identifies Clostridium difficile colitis as a serious adverse event term and gives 1.4%. These figures are counts and a registry-reported term, not a comparative safety analysis.

The record also lists other adverse events for 36 participants in the trimethoprim-sulfamethoxazole group and 39 in the placebo group. These are separate from the serious-event counts in the registry display. The record does not provide enough detail to determine event severity categories beyond the serious and other groupings, individual event patterns, or how events were judged related to treatment.

Deaths are not reported in the registry record. The small number of serious events means these figures alone provide limited information about uncommon harms or between-group differences. They should be read as the adverse-event counts posted for this trial, not as evidence that one regimen is safer or less safe overall.

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

The primary outcome counts show treatment success recorded in both randomized groups, with the re-calculated point estimate slightly higher in the group receiving trimethoprim-sulfamethoxazole in addition to cephalexin. The uncertainty around that estimate is broad. The sponsor's analysis is the official posted analysis and takes precedence because the discrepancy flag is true, but its reported p-value and interval are not readily reconciled with the re-calculation or with one another using the information in the registry.

These results do not establish a precise size or direction of the difference. The confidence intervals include the null value, and the re-calculated interval also permits effects in either direction. The sponsor's reported p-value is inconsistent with the re-calculated p-value. The reason for this discrepancy, the full analysis-population definition, and the handling of missing outcomes are not reported in the registry record.

The trial addresses a specific comparison: adding trimethoprim-sulfamethoxazole to cephalexin versus adding placebo to cephalexin for adults with uncomplicated cellulitis treated in emergency departments. It does not compare the two antibiotics as replacements for each other, and the posted data do not by themselves establish how results would apply to other populations, settings, or treatment regimens.

The registry hypothesis anticipated higher cure rates with the added antibiotic, but the hypothesis should not be confused with the observed evidence. The posted outcomes describe what was recorded in this trial; uncertainty, analysis choices, outcome definitions, and reporting completeness all affect how strongly the results can be interpreted. No medical recommendation follows from these statistical summaries alone.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment effect should be read together with its uncertainty and the analysis that produced it. A point estimate can favor one group while the confidence interval remains broad and covers values on either side of no difference. Reporting only the point estimate would obscure the limits of precision.

It also shows why consistency between an official analysis and a transparent re-calculation matters. The posted sponsor analysis and the unadjusted calculation from the group counts yield different p-values, and the registry record does not explain the difference. Stating which analysis takes precedence while retaining the discrepancy is more informative than silently choosing one result or implying that the values agree.

The endpoint definition contributes to interpretation as much as the statistical test. Treatment success incorporates subsequent hospitalization, antibiotic change, drainage, or recurrence, rather than relying only on a single examination. The definition also specifies the assessment and confirmation timeframes, making clear which events affect classification.

Finally, the record highlights the importance of complete reporting. The analysis-population description is truncated, and details about missing data, multiplicity, the original sample-size justification, and the analysis plan are not reported in the registry record. Those omissions constrain reproducibility and make it harder to distinguish an analysis discrepancy from a difference in populations or methods. Statistical transparency is essential for judging what the reported result can support.

19. 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 trial enrolled 153 participants, and the primary comparison has 73 participants in each posted arm. The resulting estimates have limited precision, as reflected in the broad confidence intervals. The registry's reported primary analysis and the unadjusted re-calculation disagree, and the record does not explain the cause or provide sufficient detail to reproduce the sponsor's result.

The registry description of the analysis population ends mid-word after referring to an intent-to-treat analysis. Although it describes several exclusions, loss to follow-up, and withdrawal, it does not give a complete definition of the population used for the posted results. Methods for handling missing endpoint information are not reported in the registry record.

The record does not report the original sample-size justification, the detailed statistical analysis plan, multiplicity procedures, or whether analyses were adjusted for baseline variables. The specific parties covered by triple masking and the randomization procedures are also not described. These omissions limit assessment of analysis choices and reproducibility.

The intended population is adults with uncomplicated cellulitis treated in an emergency department. Generalization beyond that population or beyond the shared cephalexin regimen is not established by the registry results. The secondary outcome information is limited to one posted measure, and the serious adverse event count is sparse. These features constrain the strength and scope of conclusions that can be drawn from this record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of New Antibiotic Regimen for the Treatment of Uncomplicated Cellulitis in Emergency Department Patients — NCT00676130.
• Registry record last updated 2012-08-14; status last verified 2012-08.
• Results first posted 2012-08-14.
• 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.

23. Record Summary

The registry describes a completed, randomized, parallel-group, triple-masked trial of trimethoprim-sulfamethoxazole versus placebo, each added to cephalexin, for uncomplicated cellulitis in emergency department patients. It records 153 randomized participants and a primary treatment-success outcome assessed at 12 +/- 2 days and confirmed at 30 +/- 2 days.

The posted primary results include a sponsor-reported chi-squared analysis and a separate unadjusted re-calculation from the group counts. They disagree; the sponsor's own analysis takes precedence, and the registry record does not explain the discrepancy. The reported confidence intervals are broad, and key details about the analysis population, missing data, multiplicity, and original design assumptions are not reported in the registry record.