Study to Compare Delafloxacin to Moxifloxacin for the Treatment of Adults With Community-acquired Bacterial Pneumonia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Compare Delafloxacin to Moxifloxacin for the Treatment of Adults With Community-acquired Bacterial Pneumonia (NCT02679573), a randomized phase 3 study. The primary outcome is Early Clinical Response.

2. Clinical Question

This is a comparison of assigned treatment strategies, not simply of two medications given identically to every participant. The comparator strategy allowed linezolid for confirmed MRSA, while the delafloxacin strategy allowed an intravenous-to-oral switch. The posted primary results count participants meeting the early-response definition in each randomized arm.

3. Trial Design

The registry describes a phase 3, multicenter, randomized, double-blind, comparator-controlled study with a parallel design. Its masking entry is triple. The study status is completed, and the registry lists enrollment of 860 participants. The listed start date is 2016-12-14 and the primary completion date is 2018-07-31.

Participants were assigned to delafloxacin or to the moxifloxacin/linezolid comparator strategy. Delafloxacin was given intravenously with the potential to switch to oral delafloxacin. The comparator involved intravenous moxifloxacin with the potential to switch to oral moxifloxacin, and a potential switch from moxifloxacin to intravenous linezolid for confirmed MRSA. The registry lists delafloxacin, moxifloxacin, and linezolid as drug interventions.

The primary endpoint was early clinical response in the intent-to-treat population. The registry defines that population as all randomized patients with a signed informed consent form and states that participants were analyzed according to their randomized arm. The primary assessment took place 96 (+/- 24) hours after the first dose of study drug.

Other listed outcomes include clinical outcome at test of cure, clinical outcome at end of treatment, microbiologic response, all-cause mortality, and early clinical response combined with improvement in vital signs and no worsening of the 4 symptoms. The registry lists 6 outcome measures and 6 analyses, and 5 secondary outcomes have posted results. The original design assumptions, including any sample-size justification, are not reported in the registry record.

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: 860 subjects were planned to be enrolled in the study but 859 are included in the ITT population. One subject mistakenly was randomized into the IXRS but did not provide informed consent; therefore, this subject was not included in the ITT population.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT (intent-to-treat) Population is all the randomized patients with a signed Informed consent form. Subjects were analyzed according to the treatment arm to which they were randomized.

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: ITT Population comprised all randomized subjects with a signed ICF. Subjects were analyzed according to the treatment arm to which they were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Early Clinical Response, measured over 96 (+/- 24) hours after the first dose of study drug.

The primary endpoint, early clinical response, records whether a participant met a symptom-based response definition at 96 (+/- 24) hours after the first dose of study drug. The investigator assessed chest pain, frequency or severity of cough, amount and quality of productive sputum, and difficulty breathing. Response required improvement in at least 2 of these symptoms, with no worsening of the others.

Each symptom was assessed on a 4-point scale: Absent (0), Mild (1), Moderate (2), or Severe (3). Improvement meant a decrease of at least 1 point from baseline. The endpoint is therefore a binary participant-level outcome: each person either met the response definition or did not.

An early clinical endpoint can describe short-term symptom response at a prespecified time after treatment begins. It is distinct from outcomes assessed later, such as clinical outcome at test of cure or all-cause mortality at Day 28 (+/- 2 days). The registry also lists an outcome combining early clinical response with improvement in vital signs and no worsening of the 4 symptoms; that is not the definition used for the primary endpoint.

Because this endpoint depends on investigator assessments of symptoms, the resulting counts describe whether the recorded criteria were met. They do not by themselves explain which individual symptoms changed, the size of any change beyond the threshold, or the later course of each participant.

7. Results Posted in the Registry

• Moxifloxacin/Linezolid: 89.0% (381/428) versus 88.9% (383/431) on control; risk difference 0.2 percentage points (95% CI -4.0 to 4.4), risk ratio 1.00 (0.96–1.05); unadjusted two-proportion z-test p = 0.942.

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.

Microbiologic Response

• 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:
  • Moxifloxacin/Linezolid: 89.4% (235/263) versus 89.9% (231/257) on control; risk difference -0.5 percentage points (95% CI -5.8 to 4.7), risk ratio 0.99 (0.94–1.05); unadjusted two-proportion z-test p = 0.843.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Moxifloxacin/Linezolid and the control. The interval gives the range of effects that remain compatible with the data.

All-cause Mortality

• 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:
  • Moxifloxacin/Linezolid: 1.4% (6/428) versus 1.9% (8/431) on control; risk difference -0.5 percentage points (95% CI -2.1 to 1.2), risk ratio 0.76 (0.26–2.16); unadjusted two-proportion z-test p = 0.599.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Moxifloxacin/Linezolid and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the assessment beyond early symptom response. The registry lists clinical outcomes at test of cure and end of treatment, a combined early-response and vital-sign outcome, microbiologic response, and all-cause mortality. Posted results are available for 5 secondary outcomes, including microbiologic response and all-cause mortality.

Across the posted binary comparisons, the estimates do not supply a clear, precise separation between the treatment strategies: the reported confidence intervals include zero. This general pattern is consistent with the primary comparison's uncertainty, but secondary outcomes do not independently establish the primary result or resolve uncertainty about it. They address different outcome definitions and, in some cases, different assessment times or analysis populations.

Results from multiple endpoints need cautious interpretation. When several outcomes are examined, the chance of finding an apparently notable result by chance can increase if each is interpreted without adjustment. The registry record does not report whether a multiplicity strategy was planned or applied. Accordingly, unadjusted secondary comparisons carry less weight than the primary endpoint for confirmatory claims, particularly when each estimate is considered in isolation.

Secondary findings can still help describe the breadth of the posted evidence and identify outcomes that warrant further study. Their interpretation depends on the endpoint definition, timing, available participants, and analysis method. Those details are not complete for every secondary result in the registry record, so the overall pattern is more informative than treating any one secondary comparison as decisive.

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

• Early Clinical Response Plus Improvement in Vital Signs and no Worsening of the 4 Symptoms
• Clinical Outcome at Test of Cure
• Clinical Outcome at End of Treatment
• Microbiologic Response
• All-cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference represent?

A risk difference compares the proportion of participants with an event in one arm with the proportion in another. For this primary endpoint, the event is meeting the early clinical response definition. A value near zero indicates that the observed proportions are close; a positive or negative value indicates the direction of the contrast according to the selected arm order. It is an absolute comparison on the proportion scale, not a relative risk.

The recalculated primary risk difference is 0.002 for the comparison of moxifloxacin/linezolid with delafloxacin. The posted arm proportions are 0.890 and 0.889 in that order. The calculation uses the posted participant counts and arm sizes and is an unadjusted re-calculation from summary statistics. It does not account for covariates or additional trial-level information that may have been used in the sponsor's analysis.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimate. In general, it gives a range of values compatible with the observed data under the assumptions of the analysis. The recalculated 95% confidence interval for the primary risk difference runs from -0.040 to 0.043. Because it includes zero, the data do not rule out a zero difference under this calculation. Its limits also show that the estimate is not infinitely precise: meaningful differences in either direction remain compatible with the summary data.

A confidence interval is not a guarantee that the true value lies within its limits, nor does it give the probability that a particular value is true. It describes uncertainty conditional on the method and assumptions. The registry does not identify the method used for the sponsor's primary non-inferiority analysis, so the sponsor's interval and the recalculated interval should be understood as results from distinct reported approaches.

How should a p-value be read?

The unadjusted p-value for the recalculated primary comparison is 0.942. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. A large p-value does not prove equality or equivalence.

The registry's primary reported analysis is labelled non-inferiority, but the analysis details do not include a p-value or a stated method. The recalculated p-value is an unadjusted comparison based on posted summary statistics; it is not a substitute for the sponsor's analysis or for the non-inferiority margin. That margin is necessary for interpreting whether the reported interval satisfies a non-inferiority criterion.

Why does the analysis population matter?

The primary population is the intent-to-treat population defined in the registry as all randomized patients with a signed informed consent form. Participants were analyzed according to randomized arm. This preserves the comparison by assigned treatment strategy in the posted primary analysis, including the possibility of treatment switches described for the arms.

The registry record does not report the details of missing primary outcome data, imputation, sensitivity analyses, or exclusions beyond the stated population definition. It also does not report analysis populations for every secondary outcome. Those details matter because the handling of participants without an observed endpoint can affect estimates and their uncertainty.

What is different about non-inferiority?

A non-inferiority analysis asks whether the data exclude a prespecified degree of disadvantage for one treatment relative to another. It is not established simply because an ordinary difference test is not statistically significant. The prespecified margin defines how large a difference could be accepted for that purpose, and the confidence interval is interpreted against that margin. The registry record reports a non-inferiority analysis and its interval, but the margin and method are not reported in the registry record. Therefore, the posted summary does not allow a full independent evaluation of the non-inferiority criterion.

Why can over-dispersion matter?

Over-dispersion is a general issue for count outcomes when variability exceeds what a chosen statistical model expects. It can make uncertainty estimates too narrow if the model assumes less variability than the data support. The posted primary outcome is binary and summarized as participant counts, not as a dispersed count-rate outcome. The registry record does not report an over-dispersion assessment or a modeling approach for the primary endpoint, so it is not possible to say whether this issue was assessed in the sponsor's analysis.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.002, and its 95% confidence interval ranges from -0.040 to 0.043. The interval crosses zero, so the data are compatible with a small difference in either direction as well as with no difference under the recalculation. The interval's span is an important part of the result: the estimate is close to zero, but the summary data do not pin down the difference to a single precise value.

The sponsor-reported non-inferiority analysis gives a difference in responder rates of -0.2, with a 95% confidence interval from -4.4 to 4.1. The registry does not report the non-inferiority margin or analysis method. As a result, the limits can be described, but their relationship to the trial's non-inferiority criterion cannot be fully evaluated from the record.

Confidence intervals describe statistical uncertainty under the analysis assumptions, not all sources of uncertainty. They do not address whether the population represents other settings, whether endpoint assessments were consistently recorded, or how missing observations were handled. Those details are not reported in the registry record.

For the secondary outcomes with posted comparisons, the intervals also include zero. Those estimates are less conclusive when considered alongside the number of outcomes and the absence of a reported multiplicity strategy. Precision should therefore be judged from the estimates and their intervals, not from whether a single p-value crosses a 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 sample-size illustrations use the observed effect as a starting point and show how the required sample size changes when planning to detect the full observed effect or a stated fraction of it. For these binary participant outcomes, the figures are participants per arm. The general convention for a time-to-event planning table is different: it gives the total number of events. The posted sample-size assumptions specify 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 80% power column means the planned design would have an 80% chance of detecting the specified effect under those assumptions if that effect were the true one. The 90% power column expresses the same planning idea with a higher target chance of detection. Neither column describes the chance that the observed trial result is correct. For the primary endpoint, the illustration for 100% of the observed effect gives 637,877 participants per arm for 80% power and 853,935 participants per arm for 90% power. These are planning illustrations, not the observed enrollment.

Rows for 75% and 50% of the observed effect illustrate that smaller effects require more participants to detect under the stated assumptions. For example, planning for 50% of the observed effect gives 2,559,363 participants per arm for 80% power and 3,426,261 participants per arm for 90% power for the primary endpoint. The curve represents this relationship between the assumed effect size and the planning requirement; it is not a record of outcomes observed in the trial.

This is not observed power. The trial's original design assumptions and sample-size justification are not reported in the registry record. The illustrations are calculated from the observed effect using the stated planning assumptions and should not be read as evidence that the trial was designed with those sample sizes or that it had a particular probability of success.

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 = 0.889; treatment proportion p₁ = 0.890; average p̄ = 0.889.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4435 = 0.8693.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4435 = 0.3733.
4. n = (0.8693 + 0.3733)² / (0.0016)² = 637,876.3, rounded up to 637,877 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 <- 0.888631090487239                          # control proportion
p1 <- 0.89018691588785                          # 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(2679573)
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 = 637,877 (80% power), 853,935 (90% power)
 75% of observed effect: n per arm = 1,135,749 (80% power), 1,520,446 (90% power)
 50% of observed effect: n per arm = 2,559,363 (80% power), 3,426,261 (90% power)
power.prop.test: 637876.3 
Simulated power at n = 637,877 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as a non-inferiority comparison of responder rates. The reported difference is -0.2, with a 95% confidence interval from -4.4 to 4.1. The method and p-value are not listed, and the non-inferiority margin is not reported in the registry record.

The separate recalculation uses the posted counts and arm sizes to estimate an unadjusted risk difference of 0.002, with a 95% confidence interval from -0.040 to 0.043 and an unadjusted p-value of 0.942. These are simple re-calculations from posted summary statistics, not a reproduction of the sponsor's full analysis. The reported analyses use different displayed scales, so their values should not be compared without attention to scale.

The registry does not flag a discrepancy between the posted sponsor analysis and the recalculation. The sponsor's non-inferiority analysis remains the relevant reported analysis for that question, while the recalculation offers a transparent, unadjusted comparison based on the available counts. Because the margin and analysis details are absent, neither the recalculation nor the reported interval alone can show whether the sponsor's prespecified non-inferiority criterion was met.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 6 outcome measures and 6 analyses, with 5 secondary outcomes having posted results. Multiple outcomes can create a multiplicity problem: when many comparisons are examined, some may appear unusual by chance even if there is no underlying difference. General approaches include prespecifying a hierarchy, adjusting significance thresholds, or treating secondary analyses as exploratory. The registry record does not report whether any such strategy was used.

The primary endpoint is identified as early clinical response in the intent-to-treat population. The stated population includes all randomized patients with a signed informed consent form, analyzed according to randomized arm. This definition clarifies the primary grouping, but it does not describe how missing outcome measurements were handled.

Missing-data methods, the number of participants with unobserved primary outcomes, and sensitivity analyses are not reported in the registry record. The record also does not report whether additional per-protocol or other analysis populations were used for the non-inferiority assessment. These omissions limit the ability to assess how robust the results are to missingness or to choices about which participants were included.

The non-inferiority result is especially dependent on analysis details, including the margin and the analysis population. The registry reports the result as non-inferiority but does not report the margin or method. The record also does not report interim analyses, monitoring plans, or the original sample-size justification. Their absence from the registry record should not be taken as evidence that such procedures were or were not used; it means they cannot be assessed from the posted information.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pulmonary embolism (0.9%), pneumonia (0.7%), septic shock (0.7%), cardiac failure (0.5%), cardiac failure acute (0.5%).

For serious adverse events, the registry lists 429 participants at risk in the delafloxacin group, with 23 affected, and 427 at risk in the moxifloxacin/linezolid group, with 20 affected. These are participant counts; they are not by themselves a measure of the severity, duration, or causality of each event. The record also lists other adverse events affecting 40 participants in the delafloxacin group and 30 in the comparator group.

The registry lists deaths for 8 participants in the delafloxacin group and 6 in the moxifloxacin/linezolid group. All-cause mortality is also a secondary outcome assessed at Day 28 (+/- 2 days). A count of deaths does not establish that treatment caused or prevented a death, and the record does not provide a causal assessment in these figures.

Reported serious-event terms include Pulmonary embolism (0.9%), Pneumonia (0.7%), Septic Shock (0.7%), Cardiac failure (0.5%), Cardiac failure acute (0.5%), and Chronic obstructive pulmonary disease (0.5%). These terms describe reported events and do not, by themselves, indicate comparative risk or attribution to study treatment. Safety comparisons require attention to event definitions, exposure, follow-up, and the completeness of reporting.

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

The primary results show that similar numbers of participants in the randomized arms met the registry's early clinical response definition. The recalculated risk difference is close to zero, while its confidence interval includes zero and allows differences in either direction. The data therefore do not establish that the response rates are identical; they also do not provide a precise estimate that excludes all potentially relevant differences.

The registry's sponsor-reported analysis is labelled non-inferiority, but the margin and method are not reported in the registry record. A non-inferiority conclusion depends on comparing the confidence interval with the prespecified margin, so the posted summary does not permit a complete independent appraisal of that criterion.

These results concern an early, symptom-based endpoint in the defined intent-to-treat population. They do not answer every question about later clinical outcomes, microbiologic response, mortality, or safety. The registry contains secondary results, but multiple outcomes and unreported analysis details limit how strongly they can be used to confirm or extend the primary finding.

The findings apply to the treatment strategies as described, including the potential intravenous-to-oral switches and the potential use of linezolid for confirmed MRSA in the comparator arm. They should not be generalized automatically to other populations, settings, or treatment approaches. The trial record reports a randomized comparison; interpreting the strength and scope of its evidence also requires attention to precision, missing-data handling, multiplicity, and the details of the sponsor's analysis.

Statistical uncertainty is not the same as clinical importance. Whether a possible difference would matter depends on context not established by a p-value alone. The posted summaries describe the estimates and their uncertainty, but do not provide a clinical threshold for interpreting the size of a difference.

18. Why This Trial Matters Statistically

This trial is statistically informative because it reports a randomized comparison of two treatment strategies and defines a participant-level primary endpoint with a specified assessment window. The early-response criterion is explicit: improvement in at least 2 of 4 symptoms, with no worsening of the others, assessed 96 (+/- 24) hours after the first dose. That definition helps readers understand what the response counts represent.

The comparison also illustrates why an estimate and its precision must be considered together. The recalculated point estimate is close to zero, but the confidence interval remains compatible with differences in either direction. A near-zero estimate is not proof of equivalence, and a non-significant unadjusted p-value is not proof that no difference exists.

The record also distinguishes an ordinary unadjusted comparison from a reported non-inferiority analysis. That distinction matters: non-inferiority requires a margin and an analysis plan, neither of which is reported in the registry record. The posted summary gives the sponsor's interval but does not give enough detail to independently check the criterion.

Finally, the secondary outcomes, safety counts, and planning illustrations show how different kinds of evidence answer different questions. Secondary comparisons can broaden the picture but require caution in the presence of multiple outcomes. Safety counts describe reported events rather than causality. Sample-size illustrations are prospective planning tools based on assumptions, not measures of the evidence observed in this completed trial.

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 or the method used for the sponsor's primary analysis. These omissions prevent an independent check of the non-inferiority criterion from the posted summary. The reported analysis also lacks a listed p-value.

Details on missing primary outcome data, imputation, sensitivity analyses, and the handling of missing values are not reported in the registry record. The primary population definition is stated, but the number of participants with missing outcome assessments and any additional analysis populations are not described in the posted results.

The record lists multiple outcomes and analyses but does not report a multiplicity plan. This limits interpretation of secondary comparisons, especially if they are treated as confirmatory. The registry also does not report interim analyses, monitoring details, or the original sample-size justification.

The primary outcome is based on investigator-rated symptoms and a threshold for improvement. The posted summary does not give the distribution of symptom scores or the pattern of changes across individual symptoms, so it cannot show how participants met or failed the composite response definition. The registry record also does not provide enough detail to assess the consistency of those assessments across sites.

The comparison concerns treatment strategies that allowed treatment switches, including possible linezolid use for confirmed MRSA in the comparator arm. The posted summaries do not report how many participants switched treatments. This limits the ability to describe actual treatment exposure from these aggregate results. These points qualify interpretation of the posted estimates; they do not negate the randomized comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Compare Delafloxacin to Moxifloxacin for the Treatment of Adults With Community-acquired Bacterial Pneumonia — NCT02679573.
• Registry record last updated 2020-02-27; status last verified 2020-02.
• Results first posted 2020-02-27.
• 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

NCT02679573 is a completed phase 3, multicenter, randomized, double-blind, comparator-controlled parallel study in adults with community-acquired bacterial pneumonia. The registry lists enrollment of 860 and compares intravenous-to-oral delafloxacin with a moxifloxacin strategy that could include a switch to intravenous linezolid for confirmed MRSA.

The primary endpoint was early clinical response in the intent-to-treat population, assessed 96 (+/- 24) hours after the first dose. The posted counts were 383 of 431 for delafloxacin and 381 of 428 for moxifloxacin/linezolid. The recalculated risk difference is 0.002, with a 95% confidence interval from -0.040 to 0.043.

The registry reports a non-inferiority analysis but does not report its margin or method. Missing-data handling, multiplicity strategy, and original sample-size justification are also not reported in the registry record. These gaps limit independent assessment of the analysis beyond the posted summaries.