Comparative Study To Determine The Efficacy, Safety, And Tolerability Of Ceftolozane-Tazobactam: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Study To Determine The Efficacy, Safety, And Tolerability Of Ceftolozane-Tazobactam (NCT03485950), a randomized phase 2 study. The primary outcome is Number of Participants With Favorable Clinical Response at End of Inpatient Intravenous Therapy (EOIV).

2. Clinical Question

3. Trial Design

The registry describes NCT03485950 as a Phase II, randomized, open-label, prospective, parallel-group study conducted at a single center. M.D. Anderson Cancer Center is listed as the sponsor. The study status is completed, and the registry enrollment is 100. The recorded study start is 2018-05-16 and the primary completion date is 2021-05-01.

Participants were assigned to ceftolozane-tazobactam or standard-of-care antibiotic treatment. The ceftolozane-tazobactam arm received intravenous treatment every 8 hours for up to 14 days, unless disease progression or unacceptable toxicity occurred. The protocol description allowed a switch to other oral or intravenous antibiotics at the study doctor’s discretion after at least 3 days. Standard-of-care treatment could consist of cefepime, meropenem, or piperacillin-tazobactam, with the specific administration schedules stated in the arm description.

The study was open-label, so treatment assignment was not masked according to the registry. The registry describes randomization but does not report the sequence-generation method, allocation concealment, or stratification factors. Those details are not reported in the registry record. The record identifies adults with cancer and febrile neutropenia as the target population and describes the study as investigational for this use of ceftolozane-tazobactam.

Enrollment of 100 is the registry’s planned or recorded enrollment figure; the primary outcome data use the MITT analysis set, with 47 participants in the ceftolozane-tazobactam arm and 50 in the standard-of-care arm. These outcome denominators should be read as analysis-set counts, not as a complete account of participant flow. Reasons for any difference between the enrollment figure and the outcome denominators 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Patients in MITT (Modified Intent-To-Treat) Analysis Set

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: Patients in Modified Intent-To-Treat (MITT) analysis set

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Favorable Clinical Response at End of Inpatient Intravenous Therapy (EOIV), measured over Within 72 hours after administration of the last dose of inpatient IV study drug.

The primary endpoint counts participants with a favorable clinical response at the end of inpatient intravenous therapy, abbreviated EOIV. The assessment was made within 72 hours after the last dose of inpatient intravenous study drug. The registry defines favorable response using clinical status and the need for further antibacterial treatment: acute signs and symptoms of the primary infection had to resolve or improve sufficiently that additional antibacterial therapy was not required, apart from protocol-allowed adjunctive treatment or an oral or intravenous switch, and total antibacterial therapy could not exceed 14 days.

This endpoint is a binary clinical outcome: each participant is classified as having or not having a favorable response under the stated definition. It therefore focuses on a clinically interpretable response at a specified treatment milestone rather than on a laboratory measure alone. The endpoint is assessed in the MITT analysis set, which the registry identifies as the primary population for this outcome.

The endpoint’s definition includes both symptom improvement and treatment requirements. That makes the response dependent not only on infection signs but also on decisions about additional antibiotics and permitted treatment changes. The open-label design means treatment and clinical decisions were not masked to assignment, a relevant consideration when interpreting an outcome that includes clinical assessment and treatment decisions.

7. Results Posted in the Registry

• Ceftolozane/Tazobactam Arm: 87.2% (41/47) versus 72.0% (36/50) on control; risk difference 15.2 percentage points (95% CI -0.4 to 30.9), risk ratio 1.21 (0.99–1.49); unadjusted two-proportion z-test p = 0.064.

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 Favorable Clinical Response in the Clinically Evaluable (CE) Analysis Set at EOIV.

• 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:
  • Ceftolozane/Tazobactam Arm: 93.5% (29/31) versus 84.2% (32/38) on control; risk difference 9.3 percentage points (95% CI -5.1 to 23.8), risk ratio 1.11 (0.94–1.31); unadjusted two-proportion z-test p = 0.228.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ceftolozane/Tazobactam Arm and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Favorable Clinical Response in the MITT Analysis Set at TOC

• 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:
  • Ceftolozane/Tazobactam Arm: 72.3% (34/47) versus 56.0% (28/50) on control; risk difference 16.3 percentage points (95% CI -2.4 to 35.1), risk ratio 1.29 (0.95–1.75); unadjusted two-proportion z-test p = 0.094.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ceftolozane/Tazobactam Arm and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Favorable Clinical Response in the MITT Analysis Set at Late Follow-Up (LFU)

• 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:
  • Ceftolozane/Tazobactam Arm: 70.2% (33/47) versus 52.0% (26/50) on control; risk difference 18.2 percentage points (95% CI -0.8 to 37.3), risk ratio 1.35 (0.98–1.87); unadjusted two-proportion z-test p = 0.066.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ceftolozane/Tazobactam Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary clinical-response outcomes extend the primary comparison to other assessment times and analysis populations. In the posted MITT outcomes at Test of Cure and Late Follow-Up, the favorable-response counts are higher in the ceftolozane-tazobactam arm. The clinically evaluable EOIV comparison also has a higher observed count in that arm. Across these comparisons, the intervals include no difference, so the pattern is directional but uncertain rather than a set of precise, conclusive differences.

These outcomes provide context for the primary EOIV result by asking whether the observed pattern appears at other follow-up assessments or under a different analysis-set definition. They do not replace the primary endpoint. Later assessments address response at different times, and the clinically evaluable population is not the same analysis population as the MITT set. Differences across these results can reflect timing, population definitions, or sampling variation; the record does not report enough detail to separate those explanations.

The registry lists 23 secondary outcomes, while the secondary outcome details in the record include outcomes across EOIV, Test of Cure, and Late Follow-Up and across MITT, mMITT, and clinically evaluable populations. The registry does not report a multiplicity adjustment or a hierarchy establishing which secondary comparisons were confirmatory. Because multiple outcomes can create more opportunities for apparently notable results, unadjusted secondary findings carry less weight than a prespecified primary comparison and should be regarded as supportive or exploratory.

The overall secondary pattern is broadly consistent with the direction of the primary point estimate, but it does not eliminate the uncertainty in that estimate. Nor should several related outcomes be treated as independent replications: they arise within the same trial and may involve overlapping participants or related response definitions. The registry record does not report the participant overlap across these analysis sets. The most defensible reading is that the secondary results add descriptive context without establishing a separate, definitive treatment effect.

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

• Number of Participants With Favorable Clinical Response in the Microbiological Modified Intent-to-treat (mMITT) Analysis Set at EOIV.
• Number of Participants With Favorable Clinical Response in the Clinically Evaluable (CE) Analysis Set at EOIV.
• Number of Participants With Favorable Clinical Response in the MITT Analysis Set at TOC
• Number of Participants With Favorable Clinical Response in the MITT Analysis Set at Late Follow-Up (LFU)
• Number of Participants With Favorable Clinical Response in the mMITT Analysis Set at Test of Cure (TOC)
• Number of Participants With Favorable Clinical Response in the mMITT Analysis Set at Late Follow-Up (LFU)
• Number of Participants With Favorable Clinical Response in the CE Analysis Set at TOC
• Number of Participants With Favorable Clinical Response in the CE Analysis Set at LFU.

9. Statistical Interpretation

10. Statistical Methods Explained

Clinical outcomes such as favorable response are often recorded as yes-or-no results for each participant. For this study, the registry reports counts of participants with favorable clinical response and the numbers assessed in each arm. A comparison of these counts can be expressed as a difference in the proportions of participants with the outcome, called a risk difference. The posted risk difference compares the ceftolozane-tazobactam arm with the standard-of-care arm; positive values indicate a higher observed response proportion in the former arm.

A risk difference is an absolute contrast between groups, rather than a relative measure. It is useful because it keeps the comparison on the same scale as the outcome proportion and describes the magnitude of the separation between arms. A risk ratio and an odds ratio express relative contrasts in different ways. They can be informative, but do not replace the absolute difference. The registry record also gives risk-ratio and odds-ratio estimates for the primary and selected secondary comparisons. All such measures remain estimates based on the observed participants, and their uncertainty matters alongside their point estimates.

What does a confidence interval describe?

A confidence interval gives a range of values that are reasonably compatible with the observed data under the statistical method used. It reflects sampling uncertainty: another study of the same kind could produce a different estimate. An interval that includes the no-difference value does not demonstrate that the groups are identical. It indicates that the data do not rule out no difference at the confidence level used. The interval can also include effects that could be important in either direction, so its width and endpoints matter for judging precision.

For the primary outcome, the reported risk-difference interval extends from -0.004 to 0.309. It includes zero, the no-difference value for a risk difference. The estimate points toward a higher response proportion in the ceftolozane-tazobactam arm, but the interval leaves uncertainty about the size of any difference. The posted interval is not a prediction range for individual participants and does not describe the range of all possible outcomes in future use.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.064. A p-value measures how unusual data at least as discrepant as those observed would be under a stated null model, assuming the statistical model and other test assumptions hold. It is not the probability that the null hypothesis is true, and it does not quantify the probability that the observed pattern arose by chance in a general sense. It also does not measure the size or clinical importance of a difference. The p-value needs to be interpreted with the estimate, confidence interval, analysis population, and multiplicity context.

The registry labels the comparison as unadjusted. No multiplicity procedure is listed in the registry record. When many outcomes or comparisons are examined, the chance of seeing an apparently notable result among them can increase. Without a stated adjustment or a complete testing hierarchy, secondary p-values should be considered exploratory and interpreted cautiously.

What does randomization contribute?

Random assignment is intended to make the comparison between treatment groups less vulnerable to systematic differences in participant characteristics at the start of a study. It does not guarantee that groups will be identical, particularly in a study with the posted analysis-set sizes. The registry confirms randomization but does not report the method used to generate the sequence, the concealment process, or any stratification factors. These design details are therefore not reported in the registry record.

Open-label treatment means participants and study staff were not masked to assigned treatment. This can matter when outcome assessment depends on clinical judgment or subsequent treatment decisions. The primary response definition includes symptom assessment and whether additional antibacterial therapy is required, so the absence of masking is relevant context. It does not, by itself, establish that the assessments were biased.

Why do analysis populations matter?

The primary outcome uses the MITT analysis set. The registry also reports a clinically evaluable analysis set for EOIV, and MITT outcomes at later follow-up times. These populations may include different participants according to their analysis-set definitions. The registry record does not provide the full criteria for inclusion in each set or a participant-flow account explaining exclusions. Results from different sets therefore answer related but not identical questions and should not be merged into a single summary estimate.

For a binary endpoint, the denominator is the number assessed in the specified analysis set, while the event count is the number classified as having a favorable response. A change in denominator across analysis sets or time points may reflect the definition of the set or availability of an assessment; the reasons are not reported in the registry record. The count and denominator should always be read together, and the analysis population should be identified when comparing outcomes.

The registry posts no reported analyses in the analysis records and lists no adjustment details for the posted comparisons. The displayed comparisons are therefore best understood as unadjusted summaries of the reported group data, not as evidence of a fully documented adjusted model. The record does not report covariate-adjusted estimates, a missing-data method, interim analyses, or the trial’s original statistical plan.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.152, with a confidence interval from -0.004 to 0.309. The interval crosses zero, so the data are compatible with no difference between arms as well as with differences favoring either arm. Its span also illustrates that the estimate is not highly precise: a relatively broad range of treatment contrasts remains compatible with the data.

Confidence intervals should be read as a measure of uncertainty about the group contrast, not as a guarantee that the true effect lies within the interval or as a range of individual responses. The point estimate is the center of the reported comparison, but it should not be separated from the interval. The unadjusted p-value of 0.064 is consistent with the same broad message: the observed data do not provide a sharply defined estimate that excludes no difference under the reported comparison.

The registry reports intervals for the secondary comparisons as well. Those intervals also include no difference, and they are substantial in width. The smaller analysis sets for the clinically evaluable endpoint are relevant to precision because fewer assessed participants generally yield less information about a group contrast. That general statistical principle does not determine the size of any particular interval; the posted interval is the direct summary of uncertainty for that comparison.

Precision is distinct from clinical importance. A narrow interval can estimate a small effect precisely, while a wider interval can leave considerable uncertainty about whether an effect is small or larger. The registry does not state a threshold for a clinically important difference. The posted results therefore support describing the estimated direction and uncertainty, but not declaring that the difference meets a particular clinical 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 participants per arm for the binary outcomes in this record. They are not total events. The planning illustration uses a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, and 50% of that observed effect. The original trial design assumptions and the trial’s own sample-size justification are not reported in the registry record.

The 80% power column describes the approximate number of participants per arm required for an assumed future study to have an 80% chance of detecting the stated effect under the planning assumptions, if that effect and the assumptions are correct. The 90% power column uses a higher chance of detecting that effect and consequently gives a larger planning requirement. These are prospective planning illustrations; they are not observed power.

For the primary outcome, planning for 100% of the observed effect gives 109 participants per arm for 80% power and 145 participants per arm for 90% power. Planning for 75% of the observed effect gives 208 and 277 participants per arm, respectively. Planning for 50% of the observed effect gives 496 and 663 participants per arm, respectively. The pattern illustrates a general feature of sample-size planning: smaller effects are harder to distinguish from random variation and require more participants for the same target power.

The curve should be read as a visual version of this relationship between the effect being targeted and the required sample size, under the stated assumptions. These calculations do not show what the completed trial was powered to detect, and they should not be interpreted as evidence that an effect was or was not detected. The record does not report whether the assumptions used in the planning illustration match the original design.

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 = 0.720; treatment proportion p₁ = 0.872; average p̄ = 0.796.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5697 = 1.1166.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5594 = 0.4708.
4. n = (1.1166 + 0.4708)² / (0.1523)² = 108.6, rounded up to 109 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 <- 0.72                          # control proportion
p1 <- 0.872340425531915                          # 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(3485950)
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 = 109 (80% power), 145 (90% power)
 75% of observed effect: n per arm = 208 (80% power), 277 (90% power)
 50% of observed effect: n per arm = 496 (80% power), 663 (90% power)
power.prop.test: 108.6 
Simulated power at n = 109 per arm: 0.805 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, time points, populations, or statistical comparisons. Even when each individual test uses the same nominal threshold, a larger collection of tests increases the chance that at least one result will appear unusual by chance. This matters for NCT03485950 because the registry lists 23 secondary outcomes in addition to the primary outcome, with response assessed at several time points and in multiple analysis populations.

The primary comparison is reported with an unadjusted p-value. The registry record does not report a multiplicity correction, a ranked testing sequence, or a prespecified hierarchy that would show how the primary and secondary tests were intended to be interpreted together. The registry also lists no reported analyses in the analysis records. Consequently, the p-values should not be read as adjusted evidence across the outcome family, and secondary comparisons should be treated cautiously rather than as independent confirmatory tests.

The outcome populations include MITT, mMITT, and clinically evaluable sets. The record gives some denominators but does not report the full inclusion criteria for these analysis sets, participant flow, or the reasons participants may be absent from a particular assessment. The statistical handling of missing outcomes, including any imputation or sensitivity analyses, is not reported in the registry record. Without those details, it is not possible to judge how missingness may have affected the reported estimates.

The record also does not report the trial’s original statistical analysis plan, covariate adjustment strategy, interim analyses, stopping rules, or sample-size justification. Those items should be described as not reported in the registry record, not assumed to have been absent from the study itself. Their absence from the registry limits how fully the posted comparisons can be evaluated for prespecification and analysis choices.

The primary result remains interpretable as the posted unadjusted comparison for the stated MITT endpoint. However, the relationship between that result and the wider set of outcomes cannot be fully assessed without the missing analysis details. This is an important distinction between a registry summary of results and a complete statistical report.

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (26.0%), lung infection (20.0%), fever (16.0%), bloodstream infection (12.0%), catheter related infection (8.5%).

The registry reports serious adverse events in 33 of 47 participants in the ceftolozane-tazobactam arm and 33 of 50 participants in the standard-of-care arm. Other adverse events were reported in 9 of 47 and 6 of 50 participants, respectively. The record also reports 3 deaths in the ceftolozane-tazobactam arm and 2 in the standard-of-care arm.

These are counts within the groups at risk, not estimates of whether treatment caused an event. The registry record does not provide a causal assessment for the listed events, nor does it give a comparative statistical analysis of these safety counts. The top serious-event terms are Febrile neutropenia at 26.0%, Lung infection at 20.0%, Fever at 16.0%, Bloodstream infection at 12.0%, Catheter related infection at 8.5%, and Infections and infestations at 6.4%. The registry’s event-term percentages should be read as reported; the record does not provide their denominators in the summarized information.

Safety interpretation should account for the illness being studied, the treatment context, and the fact that the study is a randomized, open-label Phase II trial at a single center. The counts describe what the registry recorded, but do not by themselves establish a difference in safety between the arms.

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

The posted primary result describes a higher observed favorable-response count in the ceftolozane-tazobactam arm than in the standard-of-care arm at EOIV: 41 of 47 compared with 36 of 50. The risk-difference estimate is positive, but its confidence interval includes zero and the unadjusted p-value is 0.064. The data therefore show a direction of difference in the observed sample while leaving substantial uncertainty about the size and reliability of the underlying contrast.

This result does not establish that ceftolozane-tazobactam is superior, equivalent, or inferior to standard-of-care treatment. An interval that crosses zero is not proof that the treatments have identical effects. Equally, a positive point estimate alone is not sufficient to establish a treatment benefit. The record does not report a threshold for clinical importance or a complete prespecified analysis framework with which to make a confirmatory claim.

The findings also do not answer every question about febrile neutropenia treatment. The study was conducted at a single center and was open-label. The primary analysis applies to the MITT set, and secondary analyses use other populations and assessment times. Generalizing beyond the population and setting studied requires evidence beyond the registry summary. The registry describes ceftolozane-tazobactam use for febrile neutropenia as investigational, while noting that the drug is approved and commercially available for certain infections.

The safety counts are descriptive and do not show whether reported events were caused by assigned treatment. The record does not report a comparative safety model or causal attribution for the events. In the same way, the secondary efficacy outcomes add context but do not overcome uncertainty in the primary comparison, particularly because their p-values are unadjusted and the multiplicity strategy is not reported.

Overall, the registry records observed clinical responses and safety events in a randomized comparison. It supports a careful description of those data and their uncertainty, not medical advice or a definitive conclusion about treatment choice.

17. Why This Trial Matters Statistically

This trial illustrates why clinical-result interpretation depends on more than comparing the response counts. The primary outcome is clinically defined and tied to a clear treatment milestone, but the resulting group contrast still has sampling uncertainty. The estimate, confidence interval, p-value, analysis population, and study design each contribute a different part of the statistical interpretation.

The result also shows the distinction between an observed difference and a precisely established effect. The ceftolozane-tazobactam arm has a higher favorable-response count in the posted MITT comparison, while the confidence interval includes no difference. A reader who focuses only on the point estimate may overstate the evidence; a reader who focuses only on whether an interval crosses zero may miss the range of effects still compatible with the data. Both magnitude and uncertainty matter.

Multiplicity is especially relevant in a trial with many secondary outcomes, assessment times, and analysis populations. Related findings may look consistent without providing independent confirmation. The absence of reported multiplicity procedures and analysis-plan details makes it important to distinguish the primary comparison from exploratory secondary patterns.

The registry also makes visible the practical role of analysis populations. A primary MITT result and a clinically evaluable result answer related but not identical questions. Denominators and outcome definitions are part of the estimand being described, not bookkeeping details that can be ignored. Open-label assessment and the clinical components of the response definition are further context for evaluating the endpoint.

Finally, planning illustrations based on an observed effect are not retrospective evidence of power or proof that the study was adequately designed. They show how future sample-size requirements can change when the target effect changes. This helps distinguish what the completed trial observed from what a future study might need to estimate an effect with greater precision.

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.

The study is Phase II and single-center, which limits how confidently the results can be generalized to other settings. It was open-label, and the primary outcome includes clinical assessment and decisions about further antibacterial therapy. These design features do not invalidate the result, but they are relevant when judging the possibility of assessment or treatment-decision effects.

The primary analysis-set denominators are 47 and 50, while registry enrollment is 100. The registry record does not provide participant flow or explain the relationship between enrollment and the analysis populations. It also does not report full criteria for MITT, mMITT, or clinically evaluable sets, or the handling of missing assessments. These omissions limit assessment of selection and missing-data effects.

The record gives an unadjusted primary comparison and selected secondary comparisons, but does not report the original statistical analysis plan, sample-size justification, multiplicity strategy, covariate adjustment, interim analyses, or stopping rules. The trial’s original design assumptions are not reported in the registry record. The planning illustration based on the observed effect is separate from those original assumptions.

The registry’s standard-of-care arm allows different antibiotics, so the comparator is a treatment strategy rather than a single fixed drug. The record does not report how many participants received each standard-of-care option. The primary endpoint also permits treatment changes and includes judgments about the need for additional therapy, which may complicate interpretation of the contrast between assigned strategies.

Safety results are reported as event counts, without a comparative model or causal attribution in the registry summary. The listed serious-event percentages are not accompanied by denominators in the summarized information. These limits mean the safety data can be described but not used alone to establish comparative risk.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparative Study To Determine The Efficacy, Safety, And Tolerability Of Ceftolozane-Tazobactam — NCT03485950.
• Registry record last updated 2022-03-15; status last verified 2022-03.
• Results first posted 2021-07-20.
• 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

NCT03485950 is a completed, randomized, open-label, Phase II, single-center, parallel-group study sponsored by M.D. Anderson Cancer Center. It compared ceftolozane-tazobactam with standard-of-care antibiotic treatment for febrile neutropenia in adults with cancer. Registry enrollment is 100.

The primary outcome was favorable clinical response at EOIV in the MITT analysis set, assessed within 72 hours after the last inpatient intravenous dose. The posted counts were 41 of 47 in the ceftolozane-tazobactam arm and 36 of 50 in the standard-of-care arm. The reported risk-difference estimate was 0.152, with a confidence interval from -0.004 to 0.309 and an unadjusted p-value of 0.064.

The secondary results show a broadly similar direction of observed response, but their intervals include no difference and the registry does not report a multiplicity strategy. The record also reports serious adverse events, other adverse events, and deaths as group counts. Missing-data methods, the original statistical plan, and the trial’s sample-size justification are not reported in the registry record.