Single Dose vs. Two Dose Regimen of Dalbavancin for the Treatment of Acute Bacterial Skin and Skin Structure Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Single Dose vs. Two Dose Regimen of Dalbavancin for the Treatment of Acute Bacterial Skin and Skin Structure Infections (NCT02127970), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Were Clinical Responders 48-72 Hours After the Initiation of Study Drug.

2. Clinical Question

The comparison concerns an early assessment of lesion response and rescue therapy, not every aspect of clinical course or later outcomes. The registry also lists a secondary outcome concerning clinical status at the end of treatment and final visit, but the primary result is the 48–72-hour response. The registry record does not report additional details about how participants were recruited, the criteria used to establish infection beyond the stated population, or the trial’s original statistical design assumptions. These details should not be inferred from the comparison alone.

3. Trial Design

This was a Phase 3, randomized, double-blind, multicenter, parallel-group study. The registry records quadruple masking but does not specify in the information presented which roles were masked. Enrollment was 698 participants. The status is completed; the recorded study start date is 2014-04-18 and the primary completion date is 2015-03-11.

Participants were assigned to single-dose or two-dose dalbavancin. The single-dose group received 1500 mg on Day 1 and matching placebo on Day 8. The two-dose group received 1000 mg on Day 1 and 500 mg on Day 8. Both regimens are described as intravenous infusions over 30 minutes. The trial’s stated aim was to compare efficacy at 48–72 hours after treatment initiation in participants with known or suspected Gram-positive acute bacterial skin and skin structure infections.

The primary analysis population was intention-to-treat: all randomized participants, whether or not they received study drug. The posted arm counts for the primary endpoint are 349 in each group, consistent with the overall enrollment of 698. The registry record does not report how the randomization sequence was generated, whether allocation was concealed, or how protocol deviations were handled. The original sample-size justification and detailed analysis plan are not reported in the registry record either.

These design features set the context for interpreting the result. Random allocation supports a comparison between the assigned regimens, while masking is intended in general to limit the influence of treatment knowledge on trial conduct or assessment. Neither feature by itself resolves uncertainty about the effect estimate or supplies details missing from the registry record. The reported result pertains to the specified early clinical-response endpoint and should not be treated as a conclusion about unreported outcomes.

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: A total of 698 participants were randomly assigned in a 1:1 ratio to the following treatment groups: Single-dose dalbavancin group, received a single dose of dalbavancin intravenous (IV) on Day 1, and a matching placebo IV on Day 8; Two-dose dalbavancin group, received dalbavancin IV on Day 1 and Day 8.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population included all randomized participants regardless of whether or not they received study drug.

5. Baseline Characteristics

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

Population: Intent-to-treat (ITT) Population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Were Clinical Responders 48-72 Hours After the Initiation of Study Drug, measured over Up to 48-72 hours after the initiation of study drug.

The primary endpoint is the percentage of participants classified as clinical responders 48–72 hours after initiation of study drug. A responder had to be alive, have received no rescue therapy for acute bacterial skin and skin structure infection before the assessment, and show a decrease of at least 20% in lesion area relative to baseline. Lesion area was defined using the longest lesion length multiplied by the longest perpendicular width. Antibiotics given for another reason did not, by themselves, make a participant a non-responder.

This endpoint combines a clinical measurement of lesion change with survival and rescue-therapy criteria. In general, such a composite definition makes the result a measure of meeting all specified response conditions, rather than a measure of lesion size alone. The early assessment offers a defined point for comparing the assigned regimens, but it does not describe the full course of illness or later status. The registry also lists clinical status at end of treatment and final visit as a secondary outcome; that outcome is distinct from the primary early-response measure.

The primary population was intention-to-treat, including everyone randomized regardless of whether study drug was received. The registry record does not report further details about handling missing lesion assessments or other missing endpoint data. The response percentages therefore need to be read alongside the endpoint definition, population, and the uncertainty around the between-group estimate.

7. Results Posted in the Registry

• Two-Dose Dalbavancin: 84.2% (294/349) versus 81.4% (284/349) on control; risk difference 2.9 percentage points (95% CI -2.7 to 8.5), risk ratio 1.04 (0.97–1.11); unadjusted two-proportion z-test p = 0.316.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the stated responder definition or does not. The reported percentages describe the share classified as responders in each randomized group. For this kind of endpoint, a risk difference expresses the difference between the two response proportions. A positive value for the posted recalculation means the two-dose group’s response proportion is higher on that scale; the interval describes uncertainty around that estimate. The recalculated estimate is 0.029, and its confidence interval runs from -0.027 to 0.085.

What does the risk difference tell us?

The risk difference keeps the comparison on the response-proportion scale. It gives an absolute contrast rather than a relative comparison. The estimated value is a single summary of the observed contrast, while its confidence interval shows the range of values compatible with the data under the calculation’s assumptions. Because the interval extends in both directions, the posted information does not pin down the direction of the underlying difference with precision. The interval is not a range of individual participant outcomes, and it does not mean that every value inside it is equally plausible.

How should the p-value be read?

The unadjusted p-value is 0.316. In general, a p-value describes how unusual results at least as discrepant as the observed result would be under a specified null model. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that either regimen is effective. The registry record does not report a full analysis method for the sponsor’s test. The posted p-value belongs to the simple unadjusted recalculation and should be interpreted in that limited context.

The planning assumptions list a two-sided significance level of 0.05 for the sample-size illustrations. That planning value is not a substitute for a complete account of the trial’s original analysis plan. The original design assumptions, including the trial’s own sample-size justification, are not reported in the registry record. The posted illustrations use a normal approximation and equal allocation between the arms; they are not evidence about the trial’s original planning process.

What do relative measures add?

The recalculation also reports a risk ratio of 1.035, with a confidence interval from 0.968 to 1.108, and an odds ratio of 1.223, with a confidence interval from 0.825 to 1.815. In general, the risk ratio compares the response proportions as a ratio, while the odds ratio compares the odds of response. These measures use different scales from the risk difference, so their numerical values should not be compared directly with it. Their intervals also indicate uncertainty and include values corresponding to no relative difference. The risk difference is often easier to connect to an absolute contrast in proportions; the ratio measures provide complementary descriptions rather than independent confirmation.

All of these recalculated measures are unadjusted summaries based on the posted counts. They do not account for covariates, stratification, site effects, or other design features unless such details are explicitly part of the calculation. The registry record does not report those details for the sponsor’s analysis. It also does not report a complete account of the statistical model, any planned subgroup analyses, or interim analyses. Those omissions limit how far the posted summaries can be interpreted as a reconstruction of the full protocol analysis.

What is the role of the non-inferiority analysis?

A non-inferiority analysis generally asks whether an intervention is not worse than a comparator by more than a prespecified margin. The margin is essential: it defines the largest disadvantage that would still be considered compatible with non-inferiority under the chosen framework. The registry labels a reported result as non-inferiority and gives a difference of -2.9 with a 95% confidence interval from -8.5 to 2.8, but the margin is not reported in the registry record. Consequently, the stated result cannot be independently evaluated against the criterion that would support a non-inferiority conclusion. No conclusion about success or failure on that objective should be inferred from the label alone.

In general, interpretation also depends on the population used for the analysis and the handling of missing outcomes. The primary population is identified as intention-to-treat, but the registry record does not report a missing-data procedure or any additional populations used for the non-inferiority analysis. This matters because different analytic populations or assumptions about missing outcomes can affect a non-inferiority assessment. The available endpoint counts and estimates support a descriptive comparison, while the unreported details leave important parts of the analysis framework unresolved.

10. Confidence Intervals and Precision

The 95% confidence interval for the recalculated risk difference is -0.027 to 0.085. It spans negative and positive values, so the data are compatible with differences favoring either group on this scale. The interval’s width reflects uncertainty in the estimated contrast; it does not establish that the true difference is zero, and it does not guarantee that the true value falls inside the interval.

The reported arm percentages are 81.4% for single-dose dalbavancin and 84.2% for two-dose dalbavancin. A point estimate alone can make a comparison look more definite than it is. The interval is important because it shows that uncertainty around the group contrast extends beyond the point estimate in both directions. The p-value of 0.316 is another summary of the data under a null model, but it does not replace the interval or describe clinical importance.

The registry’s non-inferiority result has a 95% confidence interval from -8.5 to 2.8 around a reported difference of -2.9. That interval is on the sponsor-reported scale and direction. The registry record does not report the non-inferiority margin, which is needed to interpret whether the interval satisfies a non-inferiority criterion. The recalculated interval and sponsor-reported interval should not be treated as competing estimates of exactly the same signed contrast without accounting for their opposite direction and analysis context.

Precision is also outcome-specific. These intervals concern the primary clinical-response comparison, not later clinical status or adverse events. The registry record does not report confidence intervals for the serious adverse event counts. The posted results therefore allow a more explicit assessment of uncertainty for the primary endpoint than for the safety counts.

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

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to detect the specified effect with 80% power under those assumptions. The 90% power column gives the corresponding estimate for 90% power. In general, higher target power requires more participants when the other assumptions are held constant. The rows that plan for 100%, 75%, and 50% of the observed effect show that smaller effects require more participants to detect than larger effects under the same calculation framework.

The figures are planning illustrations, not a reconstruction of the trial’s original design and not observed power. Observed power is not a useful substitute for interpreting the result’s confidence interval and effect estimate. These calculations use the observed effect as their starting point, so they depend on an estimate that is itself uncertain. They should be read as conditional planning scenarios rather than as a claim about how likely the trial was to produce a positive result.

The event-count convention matters in general: time-to-event planning figures, when present, refer to total events, whereas other planning figures refer to participants per arm. The figures for this binary percentage endpoint are participants per arm. They do not represent event counts or a combined total across arms.

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 = 0.814; treatment proportion p₁ = 0.842; average p̄ = 0.828.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5336 = 1.0458.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5332 = 0.4488.
4. n = (1.0458 + 0.4488)² / (0.0287)² = 2,720.8, rounded up to 2,721 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 <- 0.813753581661891                          # control proportion
p1 <- 0.842406876790831                          # 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(2127970)
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 = 2,721 (80% power), 3,642 (90% power)
 75% of observed effect: n per arm = 4,918 (80% power), 6,583 (90% power)
 50% of observed effect: n per arm = 11,243 (80% power), 15,050 (90% power)
power.prop.test: 2720.8 
Simulated power at n = 2,721 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Analyses Reported by the Sponsor

The sponsor-reported analysis is labeled non-inferiority and gives a difference of -2.9, with a 95% confidence interval from -8.5 to 2.8. The groups are listed in single-dose then two-dose order. The simple recalculation is oriented in the other direction, comparing the two-dose group with the single-dose group, and gives a risk difference of 0.029 with a confidence interval from -0.027 to 0.085. The direction and scale should be kept in mind when reading the two summaries together.

The recalculation uses the posted summary counts and is unadjusted. It is useful as a transparent check of the endpoint proportions, but it does not replace the sponsor’s analysis or establish that the two methods answer an identical question. The registry record does not report enough detail to reconstruct the sponsor’s analysis method. The reported non-inferiority margin is also not available in the registry record, so the sponsor’s interval cannot be assessed against that criterion using the information recorded.

The registry does not flag a discrepancy between the posted result and the recalculation. Both summaries convey uncertainty about the group contrast; neither should be presented without its direction, scale, and analysis context. In particular, the non-inferiority label does not by itself show that the trial met a non-inferiority objective.

14. Multiplicity, Missing Data and Analysis Populations

The registry record reports one primary endpoint and one posted secondary outcome: clinical status at end of treatment and final visit. It records nine outcome measures overall, but only one secondary outcome is identified as posted in the information available for this analysis. The record does not report how many statistical tests were planned for the outcomes, whether any multiplicity adjustment was planned, or how conclusions across multiple outcomes were to be controlled. Without that information, the unadjusted p-value should be read as a result for this comparison rather than as a multiplicity-adjusted finding across the full trial.

The primary population is the intention-to-treat population, including all randomized participants regardless of whether they received study drug. The primary endpoint counts are 349 participants in each group. The registry record does not report how missing assessments were handled, whether any participants had missing primary-endpoint data, or what assumptions were used for such data. A count matching the arm size does not, by itself, describe the method used to manage missing information.

The record also does not report the full statistical analysis plan, a detailed method for the sponsor’s non-inferiority analysis, the non-inferiority margin, or any interim analyses. It does not identify additional analysis populations for the primary or non-inferiority results. These omissions matter because multiplicity, missing-data assumptions, and population definitions can affect the interpretation of reported estimates and tests. They do not justify assuming that a particular method was or was not used. The appropriate reading is limited to what the registry records: an intention-to-treat primary population, a posted unadjusted recalculation, and a separately reported non-inferiority result with important analysis details not reported in the registry record.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: skin bacterial infection (0.6%), clostridium difficile colitis (0.3%), necrotising fasciitis (0.3%), renal failure acute (0.3%), pulmonary embolism (0.3%).

Among participants at risk for serious adverse events, the registry reports 7 affected participants in the single-dose group, with 349 at risk, and 5 in the two-dose group, with 346 at risk. Other adverse events are reported for 0 participants in each group. The registry also reports 1 death in each group. These are counts as recorded; the registry record does not provide confidence intervals for them in the information available for this analysis.

The listed serious adverse event terms and frequencies are skin bacterial infection at 0.6%, Clostridium difficile colitis at 0.3%, necrotising fasciitis at 0.3%, renal failure acute at 0.3%, pulmonary embolism at 0.3%, and urticaria at 0.3%. The record does not specify the group assignment for these listed terms in the information, so they should not be attributed to a particular arm.

Serious-event counts are descriptive and do not establish that an event was caused by the assigned treatment. The denominators differ for the serious-event summaries, so the at-risk counts should be read alongside the affected counts. The registry record does not report additional detail about event timing, adjudication, or causal assessment in the information.

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

The posted primary endpoint shows response percentages of 81.4% in the single-dose group and 84.2% in the two-dose group. The recalculated risk difference is 0.029 for two-dose relative to single-dose, with a confidence interval from -0.027 to 0.085. The interval spans both directions, and the unadjusted p-value is 0.316. Together, these statistics describe an uncertain contrast in early response; they do not establish superiority, equivalence, or non-inferiority.

The endpoint has a specific definition and timeframe: response at 48–72 hours required being alive, receiving no rescue therapy for the infection before assessment, and meeting the lesion-area reduction criterion. The result therefore concerns that defined early response, not every measure of infection, later clinical status, or all outcomes that might matter to participants. The registry lists a later clinical-status outcome, but the primary result cannot stand in for that outcome.

The sponsor-reported non-inferiority analysis gives a difference of -2.9 with a 95% confidence interval from -8.5 to 2.8. Because the non-inferiority margin is not reported in the registry record, the criterion needed to interpret that result is unavailable. Similar-looking response percentages should not be treated as proof of non-inferiority without the margin and analysis context.

The safety counts describe serious adverse events, other adverse events, and deaths as recorded. They do not prove or exclude a causal relationship between treatment and an individual event, and they do not substitute for a complete safety analysis. The registry record’s limited detail on event timing and assessment also constrains interpretation.

Overall, the posted information supports a descriptive comparison of two dalbavancin regimens on an early binary clinical-response endpoint, accompanied by substantial uncertainty about the contrast. It does not support claims about outcomes that are not reported, the original design rationale, or clinical decisions for an individual. Those questions require evidence and context beyond the recorded summary.

17. Why This Trial Matters Statistically

This trial illustrates why a percentage comparison should be read together with its effect estimate and confidence interval. The response percentages, 81.4% and 84.2%, are easy to compare descriptively, but the recalculated risk-difference interval extends in both directions. The apparent closeness of the point estimates therefore does not settle whether a meaningful difference exists or which direction it takes.

It also illustrates the importance of identifying the analysis question. A non-inferiority analysis requires a prespecified margin, yet the margin is not reported in the registry record. The sponsor’s reported difference and interval cannot be interpreted as meeting a non-inferiority criterion from the label alone. Knowing the endpoint, comparison direction, analysis population, and decision criterion is essential to understanding what a reported result can support.

The endpoint combines lesion-area change with survival and rescue-therapy criteria. That definition makes clear what counts as response and shows why a percentage is not simply a measure of lesion shrinkage. Its early timeframe also distinguishes it from later clinical status. Keeping endpoint definitions and timeframes explicit prevents a result from being generalized beyond the outcome it actually measures.

Finally, the planning illustrations demonstrate that sample-size estimates depend on assumptions about the effect to detect and target power. They are not observed power and do not recover the trial’s original design rationale. Together, these points show the value of separating observed results, uncertainty, design assumptions, and unreported analysis details when interpreting a clinical trial registry record.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the non-inferiority margin, so the sponsor-reported non-inferiority result cannot be assessed against its required criterion. It also does not report the sponsor’s full statistical method, the original sample-size justification, or the trial’s complete analysis plan. The unadjusted recalculation is based on posted summary counts and cannot reconstruct analyses that might have used additional design or model details.

Missing-data handling is not reported in the registry record. The primary population is defined as all randomized participants, but the available information does not describe missing assessments, protocol deviations, or any sensitivity analyses. The record also does not report whether multiplicity adjustments were planned for the multiple outcome measures.

The posted primary outcome is an early response measure with a specific composite definition. It does not describe later clinical status or all dimensions of infection outcomes. Although the registry lists a secondary outcome for end-of-treatment and final-visit status, only one secondary outcome is posted in the record. The result should not be extended to outcomes that are not reported.

Safety information is limited in the posted summary. Serious adverse event counts and deaths are recorded, but confidence intervals, event timing, and further details about causal assessment are not reported in the registry record. The listed serious adverse event terms are not assigned to a treatment group in the information presented. These limitations constrain comparisons of safety and prevent attribution of events to a regimen based on the counts alone.

Finally, the arm descriptions include renal-function qualifications but are truncated in the registry record. The complete dosing details for those qualifications are therefore not reported in the registry record and should not be inferred. These reporting gaps are specific to the available record and do not demonstrate that the underlying trial lacked additional methods or documentation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Single Dose vs. Two Dose Regimen of Dalbavancin for the Treatment of Acute Bacterial Skin and Skin Structure Infections — NCT02127970.
• Registry record last updated 2018-09-28; status last verified 2018-08.
• Results first posted 2018-08-14.
• 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.

22. Record Summary

NCT02127970 is a completed Phase 3 randomized, double-blind, multicenter, parallel-group study comparing single-dose dalbavancin with a two-dose dalbavancin regimen for acute bacterial skin and skin structure infections. Enrollment was 698. The recorded study start date is 2014-04-18 and the primary completion date is 2015-03-11.

The primary endpoint was clinical response 48–72 hours after treatment initiation in the intention-to-treat population. Response was reported for 81.4% of the single-dose group and 84.2% of the two-dose group. The unadjusted recalculated risk difference was 0.029, with a confidence interval from -0.027 to 0.085 and p = 0.316. The registry also reports a non-inferiority analysis, but the margin is not reported in the registry record.

Serious adverse events were reported for 7 participants in the single-dose group and 5 in the two-dose group; 1 death was reported in each group. The available record supports a bounded interpretation of the posted endpoint and safety summaries, with important details of the original statistical plan and analysis not reported in the registry record.