Individualized vs. Household MRSA Decolonization: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Individualized vs. Household MRSA Decolonization (NCT01814371), a randomized na study. The primary outcome is Number of Participants With Incidence of SSTI at 3 Months After Decolonization.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial comparing an individualized decolonization approach with a household approach. The registry lists masking as none and phase as not applicable. Enrollment was 474. The trial status is completed; the recorded start is 2013-04 and primary completion is 2017-02-26. Washington University School of Medicine is listed as sponsor.

The intervention descriptions distinguish the arms by which household members performed the regimen. In the individualized arm, the regimen was performed only by household members with SSTI in the prior year. In the household arm, all household members performed it. The listed components are 2% mupirocin ointment, dilute bleach baths, and a hygiene protocol. Details such as the precise application schedule or adherence measures are not reported in the registry record.

The primary outcome is the number of participants with an SSTI during the 3 months after decolonization. The registry says 447 of 474 participants were analyzed for this time frame and that the remaining 27 were lost to follow up. The primary-outcome analysis population is therefore not described as including every enrolled participant. The registry record does not report the original sample-size justification, the allocation sequence method, the original statistical analysis plan, or whether an intention-to-treat analysis was designated.

Secondary outcomes cover SSTI at other follow-up times and MRSA colonization at several follow-up times. The registry lists 14 secondary outcomes, but numerical results for every listed outcome are not available in the information analyzed. The trial design can therefore be described from its recorded arms and measures, but not supplemented with assumptions about procedures or analysis decisions that are not reported.

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:

Analysis population for the primary outcome, as defined in the registry: 447 of 474 participants were analyzed. The remaining 27 participants were lost to follow up for this time frame.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Incidence of SSTI at 3 Months After Decolonization, measured over 3 months after enrollment.

The primary endpoint counts participants with an incidence of SSTI at any time during the 3 months following the decolonization protocol. The registry gives the timeframe as 3 months after enrollment. This is a cumulative participant count over the stated follow-up period, not a count of every episode of infection. A participant with more than one episode would still contribute to the participant count as a participant with an event, according to the endpoint description.

Using an event count makes the outcome directly interpretable as whether a participant experienced the specified event during follow-up. Comparing the arms can address whether the approaches were associated with different observed event experience over that period. It does not, by itself, describe when events occurred, how many episodes each participant experienced, or the duration of time each participant remained under observation. Those details are not reported in the registry record.

For this endpoint, 23 participants in the individualized approach were reported with SSTI among 235 analyzed, and 23 in the household approach among 212 analyzed. These are the posted arm counts and denominators. The endpoint is relevant to the stated trial question because the study aimed to compare decolonization approaches in relation to prevention of SSTI. The registry’s count measure should be interpreted alongside the incomplete follow-up noted for this time frame and the uncertainty around the between-arm estimate.

7. Results Posted in the Registry

• Household Approach: 10.8% (23/212) versus 9.8% (23/235) on control; risk difference 1.1 percentage points (95% CI -4.6 to 6.7), risk ratio 1.11 (0.64–1.92); unadjusted two-proportion z-test p = 0.712.

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 With Incidence of SSTI at 1 Month After Decolonization

• 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:
  • Household Approach: 3.8% (8/212) versus 3.4% (8/237) on control; risk difference 0.4 percentage points (95% CI -3.0 to 3.8), risk ratio 1.12 (0.43–2.93); unadjusted two-proportion z-test p = 0.820.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Household Approach and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Incidence of SSTI at 6 Months After Decolonization

• 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:
  • Household Approach: 15.8% (33/209) versus 14.2% (32/225) on control; risk difference 1.6 percentage points (95% CI -5.2 to 8.3), risk ratio 1.11 (0.71–1.74); unadjusted two-proportion z-test p = 0.648.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Household Approach and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Incidence of SSTI at 9 Months After Decolonization

• 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:
  • Household Approach: 16.9% (35/207) versus 17.3% (39/226) on control; risk difference -0.3 percentage points (95% CI -7.4 to 6.7), risk ratio 0.98 (0.65–1.48); unadjusted two-proportion z-test p = 0.923.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Household Approach and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures of SSTI at follow-up times other than the primary time point, along with measures of MRSA colonization. The posted numerical SSTI summaries show event counts in both arms across the available follow-up summaries, without a consistent pattern of a large, clearly separated arm difference. The reported uncertainty for these comparisons is substantial. These outcomes offer context around the primary result but do not turn the primary comparison into evidence of equivalence.

Secondary outcomes can help describe whether the primary pattern is broadly similar across follow-up measures and related outcomes. They are not independent confirmation simply because multiple outcomes are listed: measures from the same trial can be correlated, and the same participants may contribute to more than one follow-up result. The endpoint counts and analyzed denominators also vary across the posted time-specific summaries. The registry does not report details sufficient to characterize all relationships among these observations.

The registry lists 14 secondary outcomes, but numerical results for every listed outcome are not reported in the registry record. In particular, the listed MRSA colonization outcomes should not be interpreted as showing a direction or magnitude without numerical results. The available information supports only a general reading of the posted secondary SSTI summaries, not a complete account of every secondary endpoint.

Unadjusted secondary comparisons carry less weight than a prespecified primary analysis when many outcomes or time points are examined. Looking across numerous tests increases the opportunity for apparently notable findings to occur by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary results. Secondary findings are therefore best treated as exploratory context unless a prespecified analysis plan establishes otherwise; that plan is not reported.

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

• Number of Participants With Incidence of SSTI at 1 Month After Decolonization
• Number of Participants With Incidence of SSTI at 6 Months After Decolonization
• Number of Participants With Incidence of SSTI at 9 Months After Decolonization
• Number of Participants With Incidence of SSTI at 12 Months After Decolonization
• Number of Participants Colonized With MRSA at 1 Month After Decolonization
• Number of Participants Colonized With MRSA at 3 Months After Decolonization
• Number of Participants Colonized With MRSA at 6 Months After Decolonization
• Number of Participants Colonized With MRSA at 9 Months After Decolonization

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical results include arm-level event counts, an unadjusted risk-difference recalculation, and a sponsor-reported Fisher Exact analysis labeled non-inferiority. These analyses answer related but not necessarily identical questions. Their estimates and p-values should be understood in light of the methods and details that are actually reported.

What does the risk difference describe?

A risk difference compares the proportion with an event in one arm against the proportion in the other. The recalculated estimate is expressed as household approach minus individualized approach. The estimate of 0.011 is therefore positive in that direction, while the confidence interval extends from -0.046 to 0.067. The estimate is an unadjusted comparison based on the posted group counts; it does not account for covariates or other design features through a model. No adjusted estimate is reported in the registry information used for this analysis.

The registry also supplies relative-effect measures. The reported risk ratio is 1.108, with interval limits 0.641 and 1.916. The reported odds ratio is 1.122, with interval limits 0.609 and 2.065. A risk ratio compares the event risks as a ratio, while an odds ratio compares event odds. These measures use different scales from the risk difference and should not be read as interchangeable quantities. Their intervals also include the value representing no relative difference.

What does a p-value say?

A p-value summarizes how compatible the observed data are with a specified null hypothesis under the assumptions of a particular test. It does not give the probability that the null hypothesis is true, and it does not measure the probability that a result occurred by chance. The unadjusted recalculation reports p = 0.712. The sponsor’s Fisher Exact analysis, labeled non-inferiority, reports p = 0.757. Neither value alone establishes equality of the approaches. Interpretation of a non-inferiority test requires its hypothesis, margin, direction, and analysis details; the margin and those details are not reported in the registry record.

Fisher’s Exact Test is a method for comparing categorical event data between groups. It calculates a test result using the observed arrangement of event and non-event counts, rather than relying on a large-sample approximation for the test itself. The registry identifies this method for the sponsor analysis, but does not report additional test specifications or a confidence interval for that analysis.

Why use confidence intervals?

A confidence interval shows the range of effect estimates that are reasonably compatible with the data under the interval method and its assumptions. The primary risk-difference interval crosses zero, indicating that the data do not narrowly distinguish an increase from a decrease in the household arm relative to the individualized arm. The confidence level and interval construction are not reported in the registry record, so they should not be inferred from the limits alone.

Intervals also convey precision, which a p-value does not. A p-value can be above a conventional threshold while the estimate remains uncertain over a meaningful range. Here, the interval is important because it shows that the primary estimate does not tightly rule out differences in either direction. Whether particular values in that range would be clinically important cannot be determined without a justified threshold or contextual information.

What does an unadjusted analysis leave out?

An unadjusted comparison uses the observed arm summaries without correcting for other participant or household characteristics. Randomization is intended to support a fair comparison of assigned groups, but chance imbalance can remain, and the registry information does not report a covariate-adjusted analysis. Nor does it report details about household-level clustering or how dependence among people in the same household was handled statistically. Those features may matter for precision if outcomes within a household are related, but the appropriate assessment requires design and analysis details not reported in the registry record.

The number analyzed differs by outcome follow-up time in the posted summaries. Missing follow-up can affect both the estimate and its precision, depending on why observations are missing and on the outcomes among participants not observed. The registry states that 27 participants were lost to follow up for the primary time frame but does not report imputation, sensitivity analyses, or further missing-data assumptions. As a result, these methods cannot be evaluated from the recorded results.

11. Confidence Intervals and Precision

Precision describes how tightly the data estimate the between-arm contrast. For the primary endpoint, the recalculated risk difference is 0.011 and the reported interval runs from -0.046 to 0.067. Because the interval includes zero and extends in both directions, the observed comparison does not identify a single direction with precision. It is compatible with a range of differences, not only the point estimate.

A confidence interval is a statistical tool for expressing uncertainty around an estimate under a specified method. In repeated studies using the same procedure, intervals constructed at a given confidence level would have a defined long-run coverage property. The registry record does not report the confidence level or construction method for the recalculated interval, so those details cannot be specified. The interval should not be treated as a guarantee that the true difference lies within its endpoints.

The reported relative measures also have broad intervals: the risk ratio is 1.108 with limits 0.641 and 1.916, and the odds ratio is 1.122 with limits 0.609 and 2.065. Both include the respective no-difference value. Different effect measures express the contrast on different scales, but all indicate uncertainty rather than a sharply estimated effect.

The primary analysis includes 447 of 474 participants; the registry identifies the remaining 27 as lost to follow up for this time frame. Missing observations can reduce precision and can also introduce bias if outcome availability is related to event status or arm. The registry does not describe enough about the missing outcomes to determine whether that occurred. The sponsor-reported non-inferiority p-value has no associated interval or margin in the registry record, further limiting assessment of precision relative to a non-inferiority threshold.

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 illustrations based on the observed effect, not the trial’s original design calculation. For this non-time-to-event endpoint, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original trial’s own design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect and assumptions were true. The 90% power column gives the corresponding planning target for a 90% chance. Power is a design property under assumptions; it is not a measure of how likely the observed result is to be true.

For the primary comparison, planning for 100% of the observed effect gives 12,883 participants per arm for 80% power and 17,246 participants per arm for 90% power. Planning for 75% of the observed effect gives 22,642 participants per arm for 80% power and 30,311 participants per arm for 90% power. Planning for 50% of the observed effect gives 50,357 participants per arm for 80% power and 67,413 participants per arm for 90% power. The pattern illustrates that smaller effects require more participants to detect under the same assumptions.

A sample-size curve is read by relating the assumed effect size to the required planning sample: as the effect becomes smaller, the required sample grows. These figures are not observed power and should not be interpreted as a retrospective score for the completed trial. They are planning illustrations based on the observed estimate, which itself is uncertain; they do not replace a prospective design calculation grounded in a clinically justified effect and the trial’s intended analysis.

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 = 0.098; treatment proportion p₁ = 0.108; average p̄ = 0.103.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4302 = 0.8432.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4301 = 0.3620.
4. n = (0.8432 + 0.3620)² / (0.0106)² = 12,882.5, rounded up to 12,883 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 <- 0.0978723404255319                          # control proportion
p1 <- 0.108490566037736                          # 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(1814371)
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 = 12,883 (80% power), 17,246 (90% power)
 75% of observed effect: n per arm = 22,642 (80% power), 30,311 (90% power)
 50% of observed effect: n per arm = 50,357 (80% power), 67,413 (90% power)
power.prop.test: 12882.5 
Simulated power at n = 12,883 per arm: 0.795 (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 sponsor analysis using Fisher’s Exact Test and labels it as non-inferiority. Its p-value is 0.757. The unadjusted recalculation reports a risk difference of 0.011, an interval from -0.046 to 0.067, and p = 0.712. These results come from distinct reported approaches, so their p-values need not match and should not be treated as duplicate estimates from an identical procedure.

The sponsor’s analysis is reported as a non-inferiority analysis, whereas the recalculation is a simple unadjusted comparison of the posted summary counts. The registry record does not report the non-inferiority margin, the sponsor’s full hypothesis specification, or an interval for the sponsor analysis. Without that information, the p-value cannot show whether the sponsor’s prespecified non-inferiority criterion was satisfied, nor can it establish that the approaches are equivalent.

The recalculated result is not flagged as discrepant from the posted analysis. Even so, it is not a substitute for the sponsor’s own analysis or for details missing from the registry. The sponsor analysis remains the relevant reported analysis for the trial’s stated non-inferiority framing; the recalculation offers a transparent, unadjusted description of the arm summaries and their uncertainty. Both should be interpreted cautiously and neither supports an unqualified conclusion of no difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes covering SSTI and MRSA colonization at different follow-up times. Testing several outcomes and time points creates a multiplicity issue: the more statistical comparisons considered, the greater the chance that at least one result appears notable even when there is no true effect. Appropriate interpretation depends on the study’s prespecified hierarchy and any adjustment strategy.

A multiplicity adjustment, testing sequence, or other strategy for controlling the overall false-positive risk is not reported in the registry record. The registry also does not report whether the posted secondary analyses were specified before data review. Consequently, secondary p-values, where reported, should not be read as if they were the sole planned test. This concern does not invalidate the results, but it limits how strongly isolated secondary findings can be interpreted.

For the primary time frame, the registry states that 447 of 474 participants were analyzed and that the remaining 27 were lost to follow up. It does not report why those participants were lost, whether their outcomes were sought through another method, or how missing outcomes were handled in the analysis. Imputation methods, sensitivity analyses, and assumptions about the missing outcomes are not reported in the registry record.

The denominators in the posted summaries differ by endpoint and follow-up time. The record does not give a full account of the analysis population for each measure beyond the relevant outcome summaries. It also does not state whether analyses followed intention-to-treat, per-protocol, or another specified population, including for the non-inferiority analysis. These distinctions can be important because non-inferiority conclusions may depend on the population and missing-data approach.

The registry record does not report the original statistical analysis plan, non-inferiority margin, or detailed sample-size justification. Those omissions prevent assessment of whether analyses followed the original plan and whether the trial was designed around a clinically meaningful threshold. The available results remain interpretable as posted summaries, but those design and analysis uncertainties should temper strong claims.

16. 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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry’s adverse-event summary lists 0 serious adverse events in the individualized approach among 248 participants at risk and 0 in the household approach among 226 participants at risk. It lists 0 deaths in each group. These are the serious-event and death counts recorded in the registry summary; they do not show that no other events occurred.

The same summary reports other adverse events in 41 participants at risk in the individualized approach and 102 in the household approach, with the at-risk group sizes recorded as 248 and 226, respectively. These are descriptive counts. The registry information does not provide event definitions, severity details for these other events, attribution to the regimen, or a statistical comparison. The safety denominators also differ from the primary efficacy denominators, and the reason for this difference is not reported in the registry record.

Zero recorded serious events in these groups should not be treated as proof that serious harms are impossible or that the approaches have identical safety. The summary describes observed reports within this trial and should be interpreted in that limited scope. No causal conclusion can be drawn from these counts alone.

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

The primary result describes the observed number of participants with SSTI during the specified follow-up period in the two randomized approaches. The arm counts are both 23, while the analyzed denominators are 235 for the individualized approach and 212 for the household approach. The recalculated risk difference is 0.011, with an interval from -0.046 to 0.067. The interval and p-value indicate substantial uncertainty about the size and direction of the underlying difference.

These data do not establish that the approaches are equivalent. A failure to find a statistically clear difference is not the same as demonstrating that any difference is small enough to be unimportant. A non-inferiority conclusion requires a prespecified margin and an analysis that evaluates the result against that margin. The registry record labels the sponsor’s analysis as non-inferiority but does not report the margin or enough analysis detail to judge the criterion.

The result also does not establish that either approach prevents SSTI in general. The comparison concerns these approaches, the enrolled study population, the recorded regimen, and the measured follow-up period. It cannot by itself determine how results would apply to other populations, settings, or practices. No medical advice follows from these statistical summaries.

There is further uncertainty because the primary analysis did not include all enrolled participants; 27 were reported lost to follow up for this time frame. The registry does not explain the missing outcomes or report sensitivity analyses. The posted counts are informative about the analyzed participants, but the record does not allow a full assessment of whether loss to follow up changed the comparison.

The most defensible reading is therefore descriptive and qualified: the observed primary counts are close, the estimated difference is imprecise, and the available record does not establish equivalence or non-inferiority. Broader conclusions require the missing design and analysis details, as well as consideration of the intended clinical threshold.

18. Why This Trial Matters Statistically

This trial illustrates why a similar-looking pair of event counts does not settle a comparison. The primary groups each have 23 participants with SSTI, but the denominators differ, and the recalculated estimate is accompanied by a confidence interval that spans differences in both directions. Reporting the estimate with its uncertainty is more informative than relying only on the observed counts or a p-value.

The trial also demonstrates the distinction between testing for a difference and testing for non-inferiority. A conventional difference test asks whether the evidence is inconsistent with no difference under a null hypothesis. Non-inferiority instead requires a clinically chosen margin that defines how much worse one approach could be while still meeting the study’s criterion. The registry labels the sponsor analysis as non-inferiority, but the margin is not reported. That missing design element prevents readers from translating the reported p-value into a non-inferiority conclusion.

Follow-up completeness and analysis populations also matter. The primary analysis excludes participants lost to follow up, and the record does not explain how their missing outcomes were addressed. In addition, secondary measures span multiple outcomes and time points, raising questions about multiplicity and prespecification. These are not merely technical details: they shape how much confidence a reader can place in isolated findings and in claims extending beyond the primary comparison.

Finally, planning calculations based on an observed effect can show how demanding it may be to estimate or detect small differences, but they do not reconstruct the original trial’s design rationale. Separating retrospective planning illustrations from the study’s actual design assumptions is essential to avoid overinterpreting power calculations.

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 registry record does not report the non-inferiority margin, although the sponsor’s analysis is labeled non-inferiority. Without the margin and full testing details, the central non-inferiority claim cannot be evaluated from the reported p-value alone. The confidence level and construction method for the recalculated interval are also not reported.

The primary analysis includes 447 of 474 participants, with 27 reported lost to follow up for this time frame. Reasons for loss, outcome status among those participants, and missing-data sensitivity analyses are not reported. The possibility of bias from incomplete follow-up cannot be assessed from the available record.

The registry does not report the original sample-size justification, the detailed statistical analysis plan, the planned analysis population, or the method used to generate the random allocation sequence. Masking is listed as none. Further information about adherence, crossover, treatment implementation, and household-level dependence is not reported in the registry record, limiting assessment of how the intervention was delivered and how the analysis handled related outcomes within households.

Many secondary endpoints and follow-up times are listed, but multiplicity handling and a hierarchy for interpretation are not reported. Numerical results for every listed secondary outcome are also not available in the information analyzed. Safety summaries lack event definitions and attribution details. These limitations do not erase the posted results, but they constrain causal, non-inferiority, safety, and generalizability conclusions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Individualized vs. Household MRSA Decolonization — NCT01814371.
• Registry record last updated 2019-02-21; status last verified 2019-02.
• Results first posted 2018-10-26.
• 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

NCT01814371 is a completed randomized parallel-group trial comparing individualized with household MRSA decolonization in households with children. The registry lists no masking and enrollment of 474. The primary endpoint counts participants with SSTI during the 3 months after decolonization. The primary analysis reports 23 events among 235 analyzed in the individualized arm and 23 among 212 analyzed in the household arm; 27 participants were lost to follow up for this time frame.

The unadjusted recalculated risk difference is 0.011, with an interval from -0.046 to 0.067 and p = 0.712. The sponsor-reported Fisher Exact non-inferiority analysis has p = 0.757. The registry record does not report the non-inferiority margin, original sample-size justification, detailed analysis plan, or missing-data sensitivity analyses. Results therefore describe the observed comparison but do not, on their own, establish equivalence or non-inferiority.