Safety and Efficacy of ZTI-01 (IV Fosfomycin) vs Piperacillin/Tazobactam for Treatment cUTI/AP Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of ZTI-01 (IV Fosfomycin) vs Piperacillin/Tazobactam for Treatment cUTI/AP Infections (NCT02753946), a randomized phase 2, phase 3 study. The primary outcome is Number of Patients With an Overall Success.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group study listed as Phase 2 and Phase 3. The masking designation is quadruple. The registry record names Nabriva Therapeutics AG as sponsor and describes the study as a comparative trial in hospitalized adults with complicated urinary tract infection or acute pyelonephritis. Enrollment is listed as 465, and the study status is completed.

The registry gives a start date of 2016-04 and a primary completion date of 2017-01-12. The treatment arms used intravenous ZTI-01, identified as fosfomycin, or intravenous piperacillin/tazobactam. Both regimens were administered every 8 hours over 7-14 calendar days, with different stated doses and total daily doses. The registry does not report further details about treatment duration decisions or other implementation procedures.

The primary outcome was assessed at the TOC visit on Day 19 in the m-MITT population. The posted results list 184 participants in the ZTI-01 group and 178 in the piperacillin/tazobactam group for this outcome. Those denominators should be read as the analysis groups for the reported endpoint, not as a complete explanation of how the enrolled participants moved through the study. The relationship between the enrollment figure and endpoint denominators is not reported in the registry record.

Three outcome measures are listed: overall success, clinical cure in various protocol populations, and microbiologic eradication. Two secondary outcomes are posted. The registry record does not report a detailed protocol, the randomization procedure, allocation concealment procedures, the trial's original sample-size justification, or its prespecified statistical analysis plan. Randomization and masking are recorded, but their operational details are not reported.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: At least 30% of patients required a diagnosis of AP. Receipt of effective systemic antibiotic for \>24 hrs within 72-hr window before randomization exclusionary but receiving single dose of short-acting systemic antibiotic within 72 hrs of randomization permitted up to a max of 25% of the study enrollments.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Microbiologic Modified Intent-to-Treat (m-MITT) population was used to assess overall success.

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: All subjects included (note 1 subject randomized discontinued prior to dosing). Note 6 subjects were incorrectly identified as Hispanic or Latino, instead of White in the database; errata recorded to file.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients With an Overall Success, measured over TOC Visit (Day 19).

The primary endpoint was the number of participants with overall success at the TOC visit on Day 19. Overall success required both clinical cure and microbiologic eradication of the baseline pathogen. Clinical cure was described as resolution or significant improvement in signs and symptoms; microbiologic eradication refers to the baseline pathogen. The primary analysis population was the m-MITT population.

A combined endpoint can reflect more than one dimension of response: the clinical status of the participant and the microbiologic finding. Requiring both components means that success is not counted merely because one component is present. That can make the outcome clinically interpretable as a joint response, while also making it important to understand how each component behaves separately. The registry lists clinical cure and microbiologic eradication as secondary outcomes, offering component-level information alongside the composite.

The posted endpoint is a participant count in each group. Its reported denominators are 184 for ZTI-01 and 178 for piperacillin/tazobactam. The registry record does not report details such as how incomplete outcome assessments were handled or whether participants with missing component data could be classified as having overall success. Those details matter because the endpoint depends on observing both clinical and microbiologic components at the assessment visit.

7. Results Posted in the Registry

• Piperacillin Tazobactam: 54.5% (97/178) versus 64.7% (119/184) on control; risk difference -10.2 percentage points (95% CI -20.2 to -0.1), risk ratio 0.84 (0.71–1.00); unadjusted two-proportion z-test p = 0.048.

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 Patients With a Response of Clinical Cure in Various Protocol Populations

• 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:
  • Piperacillin Tazobactam: 91.6% (163/178) versus 90.8% (167/184) on control; risk difference 0.8 percentage points (95% CI -5.0 to 6.7), risk ratio 1.01 (0.95–1.08); unadjusted two-proportion z-test p = 0.786.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Piperacillin Tazobactam and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients With a Response of Microbiologic Eradication

• 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:
  • Piperacillin Tazobactam: 56.2% (100/178) versus 65.8% (121/184) on control; risk difference -9.6 percentage points (95% CI -19.6 to 0.4), risk ratio 0.85 (0.72–1.01); unadjusted two-proportion z-test p = 0.062.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Piperacillin Tazobactam and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide a component-level view of the primary composite. Clinical cure was recorded frequently in both groups, and the reported proportions were close. Microbiologic eradication had a more noticeable descriptive separation, with the observed direction favoring ZTI-01. The primary overall-success pattern is more aligned with the microbiologic comparison than with the clinical-cure comparison, which is consistent with a composite requiring both components rather than either one alone.

These secondary findings do not independently establish a treatment effect or a non-inferiority conclusion. A secondary endpoint may be useful for understanding what contributes to a composite, but it can differ in population definitions, missingness, measurement properties, and precision. The registry lists clinical cure in various protocol populations, while detailed population rules are not reported. The secondary comparisons are unadjusted, and no multiplicity strategy or confirmatory hierarchy is reported. When several outcomes are evaluated without a stated adjustment or hierarchy, a nominally notable result has less evidential weight than a prespecified primary result interpreted under a complete analysis plan.

The secondary results should therefore be read as supportive descriptions of the posted outcome pattern. They can help distinguish clinical response from microbiologic response, but they do not resolve uncertainty about the primary finding or fill in the missing formal non-inferiority criteria. Their value is in providing context, not in replacing the primary endpoint or serving as separate proof of efficacy.

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

• Number of Patients With a Response of Clinical Cure in Various Protocol Populations
• Number of Patients With a Response of Microbiologic Eradication

9. Statistical Interpretation

10. Statistical Methods Explained

These statistical concepts are general explanations of how to read the reported binary outcomes. The registry record reports counts of participants with responses, arm denominators, risk differences, interval estimates, and unadjusted p-values. It does not report all of the methods used to produce them.

What does a response count represent?

For a binary outcome, each participant is classified as having or not having the event of interest. Here, the event is a response such as overall success, clinical cure, or microbiologic eradication. A response count is read together with its denominator: the count tells how many participants had the event, while the denominator tells how many participants contributed to that reported group result. The resulting proportion describes the observed frequency within that group. It is not, by itself, a comparison between groups.

The primary endpoint is a composite binary outcome. Its event requires both clinical cure and microbiologic eradication. A composite can summarize a combination of outcomes in a single measure, but the single result does not show which component contributed more to the comparison. The separate secondary outcomes provide context about the components, although they do not replace the primary endpoint.

How should the risk difference be read?

A risk difference is the difference between the two groups' event proportions, expressed on an absolute scale. In the posted primary comparison, the estimate is -0.102 for piperacillin/tazobactam relative to ZTI-01. A negative value means the recorded response proportion was lower in the comparator group under that ordering. The arm-specific values are 0.545 for piperacillin/tazobactam and 0.647 for ZTI-01. The estimate describes the observed contrast; it does not identify why the groups differ or establish that the contrast is caused by treatment.

Other effect measures can express a binary comparison on relative scales, such as a risk ratio or odds ratio. General interpretation differs by measure: a risk ratio compares event proportions, while an odds ratio compares event odds. A value at the measure's no-association point represents no contrast under that scale. Relative measures can look different from absolute differences because they answer different mathematical questions. The primary interpretation focuses on the posted risk difference rather than treating the different scales as interchangeable.

What does an interval estimate add?

A confidence interval expresses uncertainty around an estimated effect under a statistical procedure. It shows a range of values that are compatible with the data and assumptions of that procedure, rather than a single precise value. Narrower intervals indicate greater precision than wider intervals on the same scale. An interval that spans the no-difference value is compatible with no difference as well as with effects on either side; an interval wholly on one side indicates that the included values do not cross that reference point. These statements describe the interval, not the probability that a particular hypothesis is true.

For the primary risk difference, the reported interval is -0.202 to -0.001. The registry record does not report the confidence level or enough method detail to reproduce the interval. Its upper bound is close to zero, so the interval places the no-difference point just outside its reported range. Interpretation should retain that proximity and the uncertainty represented by the full interval, rather than focusing only on whether the bounds cross zero.

What does an unadjusted p-value mean?

A p-value summarizes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It does not give the probability that the null model is true, the probability that a result occurred by chance, or the probability that a treatment is effective. The posted primary p-value is unadjusted. That means it is not reported as corrected for evaluating multiple outcomes or comparisons. It should be interpreted alongside the estimate, interval, endpoint definition, and analysis population.

The registry record does not identify the exact test used to calculate the p-value or specify a trial-level decision threshold. The planning illustration names a two-sided significance level of 0.05, but that planning assumption is not evidence of the original trial's prespecified testing plan. The record does not report the original plan's alpha allocation, model specification, covariate adjustment, or interim-analysis procedures.

Why does the analysis population matter?

The primary endpoint description identifies the m-MITT population, or microbiologic modified intent-to-treat population. The label indicates that the primary outcome was evaluated in a defined analysis population, but its complete inclusion and exclusion rules are not reported in the registry record. Different analysis populations can answer different questions because they can include different participants or use different rules for outcome availability. The registry also lists clinical cure in various protocol populations, but detailed definitions for those populations are not reported alongside the posted results.

In randomized trials, analysis choices are important because exclusions, missing outcome data, and departures from assigned treatment can affect interpretation. The registry record does not report how missing endpoint components were treated, whether imputation was used, or which sensitivity analyses were planned. It also does not report a detailed statistical analysis plan. Therefore, the posted group counts can be described directly, but the effects of unreported population and missing-data rules cannot be assessed from this record.

Why are the secondary comparisons less definitive?

Secondary outcomes can help explain or contextualize the primary endpoint, but their interpretation depends on how they were selected and analyzed. When several outcomes are examined, the chance of at least one apparently notable result can increase if no adjustment or prespecified hierarchy is used. Multiplicity control is a statistical approach to managing that issue. The registry record does not report a multiplicity adjustment or a confirmatory hierarchy, and the secondary comparisons are listed as unadjusted. They are therefore best treated as descriptive or supportive evidence rather than as independent confirmation of the primary comparison.

Overall, the primary result is a binary-group comparison summarized using counts, proportions, an absolute risk difference, an interval, and an unadjusted p-value. Those quantities describe the posted data from complementary angles. Their interpretation remains bounded by the missing trial-specific analysis details, especially the non-inferiority margin, analysis plan, population rules, missing-data procedures, and multiplicity strategy.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.102, with reported interval bounds of -0.202 and -0.001. The interval is entirely on the negative side of zero, but its upper bound lies close to zero. This combination means that the estimated direction is consistent across the stated interval, while the precise size of the difference remains uncertain and values near no difference are close to the interval boundary. The interval also allows for a larger absolute difference in the same direction than the point estimate alone suggests.

A confidence interval is useful because it presents uncertainty in the effect estimate, not just the observed point estimate. A point estimate should not be read as the exact underlying difference. The interval's width indicates that the data are compatible with a range of possible contrasts. The registry record does not state the confidence level or the procedure used to construct this interval, so those aspects of precision cannot be independently evaluated from the record.

The unadjusted p-value of 0.048 is close to the conventional planning significance level of 0.05, but the registry's use of 0.05 is reported as a sample-size planning assumption, not as the trial's original decision rule. The result should not be reduced to a threshold judgment. The estimate, interval, unadjusted nature of the p-value, and missing non-inferiority margin all matter to interpretation.

Precision is also outcome-specific. The clinical-cure comparison has an interval spanning zero, as does the microbiologic-eradication comparison, although their point estimates differ in direction and magnitude. The primary composite combines both components and has its own uncertainty. The different intervals should not be treated as directly interchangeable, and none alone supplies the unreported analysis-plan details needed for a formal non-inferiority assessment.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original trial's own design justification. For these binary outcomes, the reported figures are participants per arm, not a total across both arms and not total events. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is the true one and the statistical model applies. The 90% power column gives the corresponding per-arm planning figure for a design with a 90% chance under the same stated conditions. These are design calculations, not guarantees about results from a future study. The columns compare different planned sample sizes for different target power levels.

Rows planning for 100%, 75%, or 50% of the observed effect represent progressively smaller target differences. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. The illustration is anchored to this trial's observed estimate; it does not establish that the observed effect is the true effect or a clinically important target.

This is not observed power. Observed power is not a measure of how persuasive or reliable the completed trial result is; the estimate and its uncertainty are more informative. The displayed planning figures should instead be read as conditional illustrations of how sample size changes when the target effect, desired power, and stated assumptions change.

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 = 0.647; treatment proportion p₁ = 0.545; average p̄ = 0.596.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6940 = 1.3602.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6903 = 0.5809.
4. n = (1.3602 + 0.5809)² / (-0.1018)² = 363.6, rounded up to 364 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 <- 0.646739130434783                          # control proportion
p1 <- 0.544943820224719                          # 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(2753946)
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 = 364 (80% power), 487 (90% power)
 75% of observed effect: n per arm = 641 (80% power), 857 (90% power)
 50% of observed effect: n per arm = 1,425 (80% power), 1,907 (90% power)
power.prop.test: 363.6 
Simulated power at n = 364 per arm: 0.799 (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

The registry record lists one primary outcome and two secondary outcomes. It reports no posted analyses in the analysis listing and no specific multiplicity adjustment, testing hierarchy, or family of hypotheses. The secondary comparisons are unadjusted. Without a stated strategy for how outcomes were prioritized and how repeated testing was handled, the secondary p-values should be interpreted cautiously. The registry record does not report whether any outcomes were prespecified as confirmatory beyond identifying the primary endpoint.

Missing-data handling is also not reported in the registry record. The primary outcome requires both clinical cure and microbiologic eradication, so interpreting the endpoint depends on how incomplete information for either component was treated. The record does not say whether missing assessments were classified as failures, excluded, imputed, or addressed through sensitivity analyses. It also does not report the extent or pattern of missing endpoint data.

The m-MITT population is named as the population used to assess overall success, but its detailed eligibility rules are not reported. The secondary clinical-cure outcome refers to various protocol populations without detailing their definitions in the posted results. Those population labels matter because analysis populations can change which participants contribute to an estimate and how the result relates to randomization. The registry enrollment is 465, while the primary outcome denominators are 184 and 178; the record does not explain the participant flow or the reasons these figures differ.

The record describes the intended non-inferiority question but does not report the non-inferiority margin, the formal testing procedure, or the original analysis plan. It also does not report interim analyses, covariate adjustment, treatment of protocol deviations, or sensitivity analyses. These are not minor details for interpreting a non-inferiority trial: they define the comparison and how robust the conclusion is expected to be. Without them, the posted counts and unadjusted comparison can be described, but the intended confirmatory framework cannot be reconstructed.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: urinary tract infection (0.4%), renal abscess (0.4%), septic embolus (0.4%), pyelonephritis acute (0.4%), renal impairment (0.4%).

The safety results list serious adverse events for 233 participants at risk in the ZTI-01 group and 231 in the piperacillin/tazobactam group. Five participants in the ZTI-01 group and six in the piperacillin/tazobactam group are reported with serious adverse events. The registry lists zero deaths in each group. These are descriptive counts within the stated safety groups; the denominators differ from those used for the primary efficacy outcome.

The serious-event terms listed in the record are Urinary Tract Infection, Renal Abscess, Septic Embolus, Pyelonephritis Acute, Renal Impairment, and Haematuria, each reported as 0.4%. The record does not provide further detail in this summary about event timing, recurrence, severity grading, or attribution to treatment. A count of participants with serious events does not by itself establish whether an event was caused by a treatment, and the listed event terms should not be interpreted as comparative risks without considering the full safety definitions and follow-up.

The safety figures are not a substitute for a full adverse-event analysis. The registry record also lists other adverse events, but the serious-event counts alone do not characterize the complete safety profile. The reported zeros for deaths describe the posted group results and should not be generalized beyond the population and follow-up recorded in the trial.

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

The posted primary data show that overall success was recorded for 119 of 184 participants receiving ZTI-01 and 97 of 178 receiving piperacillin/tazobactam at the TOC visit on Day 19. The reported risk difference is -0.102 for piperacillin/tazobactam relative to ZTI-01, with interval bounds from -0.202 to -0.001 and an unadjusted p-value of 0.048. These statistics describe the observed comparison and its uncertainty; they do not, on their own, answer every clinical or regulatory question raised by the trial.

In particular, the record describes a non-inferiority objective, but the non-inferiority margin and formal analysis procedure are not reported. A non-inferiority conclusion depends on comparing the treatment difference with a prespecified acceptable margin, not simply on whether a conventional difference test crosses a threshold. The available result therefore cannot be treated as a complete demonstration of non-inferiority from the registry entry alone.

The comparison also does not establish why the groups had different observed response counts. Randomization is part of the recorded design, but the registry's posted results do not provide the complete analysis plan, missing-data approach, population definitions, or sensitivity analyses needed to assess all sources of uncertainty. Secondary outcomes offer context about clinical cure and microbiologic eradication, but they are unadjusted and do not replace the primary analysis.

Nor should the estimate be taken as a guarantee that the same contrast would occur in another population or setting. The registry describes hospitalized adults with complicated urinary tract infection or acute pyelonephritis and the stated intravenous regimens. The reported outcome is measured at a specified TOC visit, and the safety counts are reported for different denominators. Interpretation should remain tied to these participants, outcomes, and recorded follow-up, rather than being generalized beyond the information in the registry record.

Overall, the statistics support a careful description of the trial's posted endpoint comparison. They do not independently determine treatment choice, provide medical advice, or establish that either regimen is clinically preferable. Such judgments require evidence and context beyond the posted summary statistics.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its primary endpoint combines a clinical outcome with microbiologic eradication. Composite outcomes can be useful when a study asks about more than one dimension of response, but they can conceal differences in how their components behave. Here, the clinical-cure comparison is close between groups, while microbiologic eradication has a more noticeable descriptive separation. Reading the components alongside the composite helps clarify what the overall-success measure captures without replacing it.

The study also illustrates why the estimand and analysis population matter. Overall success was assessed in the m-MITT population, yet the registry does not give the detailed population rules or explain the relation between enrollment and the endpoint denominators. Those choices can influence which participants inform the result. Transparent reporting of participant flow, endpoint availability, and analysis-population definitions is important to understanding how a randomized comparison was carried out.

Non-inferiority questions require particular attention to the prespecified margin and analysis plan. The registry states the study's non-inferiority purpose but does not report the margin or the formal decision procedure. The risk difference and its interval are informative, but they cannot stand in for the missing criteria. This is a useful distinction between a descriptive treatment-group contrast and a formal conclusion about non-inferiority.

Finally, the unadjusted secondary findings illustrate the role of multiplicity. Component outcomes can enrich interpretation, yet their evidential weight depends on how they were prioritized and whether multiple testing was addressed. The record does not report that framework. Taken together, the trial shows why effect estimates, uncertainty intervals, endpoint construction, analysis populations, and prespecified decision rules all need to be read as parts of a statistical argument rather than as isolated numbers.

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.

Several limitations specific to this trial's registry entry constrain interpretation. The stated aim was to assess non-inferiority, but the non-inferiority margin is not reported. Without the margin and formal decision rule, the primary comparison cannot be used to determine whether the prespecified non-inferiority criterion was met. The original sample-size justification and trial-specific power assumptions are also not reported; the available planning illustration is based on the observed effect and does not document the original design.

The registry does not report the detailed statistical analysis plan, exact test used for the primary comparison, confidence level for the intervals, covariate adjustment, or interim-analysis procedures. It records zero posted analyses in the analysis listing, and no sponsor analysis is separately presented there. This limits assessment of whether the posted calculation corresponds to the planned confirmatory analysis.

The m-MITT population is named, but its full definition and participant flow are not reported. Enrollment is listed as 465, whereas the primary endpoint denominators are 184 and 178; the registry record does not explain this relationship. Missing-data handling for the composite's clinical and microbiologic components is also not reported, nor are missingness patterns or sensitivity analyses. As a result, the possible influence of incomplete observations cannot be assessed from the entry.

Two secondary outcomes are posted, but their analysis-population details and any multiplicity procedure are not reported. Their unadjusted comparisons should not be treated as confirmatory evidence without knowing the planned hierarchy. Safety reporting gives group-level serious-event counts and selected terms, but does not provide the full contextual information needed to assess timing, attribution, or the complete safety profile. These limitations concern the available registry reporting and should not be mistaken for proof that particular procedures were or were not conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of ZTI-01 (IV Fosfomycin) vs Piperacillin/Tazobactam for Treatment cUTI/AP Infections — NCT02753946.
• Registry record last updated 2019-03-07; status last verified 2019-03.
• Results first posted 2018-12-11.
• 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

NCT02753946 records a completed randomized, double-blind, parallel-group Phase 2 and Phase 3 study of intravenous ZTI-01 versus piperacillin/tazobactam in hospitalized adults with complicated urinary tract infection or acute pyelonephritis. Enrollment is listed as 465. The primary endpoint was overall success, requiring clinical cure and microbiologic eradication of the baseline pathogen at the TOC visit on Day 19 in the m-MITT population.

Overall success was recorded for 119 of 184 participants in the ZTI-01 group and 97 of 178 in the piperacillin/tazobactam group. The posted risk difference for piperacillin/tazobactam relative to ZTI-01 is -0.102, with interval bounds from -0.202 to -0.001 and an unadjusted p-value of 0.048. The registry states a non-inferiority purpose but does not report the margin or full analysis plan. Secondary outcomes and serious adverse-event counts provide additional description, while missing-data procedures, multiplicity methods, and detailed analysis-population rules are not reported in the registry record.