Short-course Methenamine Hippurate for Prevention of Post-operative UTI: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Short-course Methenamine Hippurate for Prevention of Post-operative UTI (NCT02358993), a randomized na study. The primary outcome is Treatment of Clinically Suspected UTI - Using Intent to Treat Analysis.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-blind, parallel-group trial sponsored by the University of Pennsylvania. It enrolled 201 participants and is marked completed. The record lists the start as 2014-12 and the primary completion date as 2020-09-30. Phase is recorded as not applicable. The intended setting was prevention of post-operative UTI among patients requiring short-term catheterization after pelvic reconstructive surgery.

Participants were assigned to methenamine hippurate or ciprofloxacin. The primary analysis lists 101 participants in the methenamine group and 93 in the ciprofloxacin group. Those are the denominators attached to the posted primary outcome; they do not match the registry’s overall enrollment figure. The reason for the difference is not reported in the registry record. Safety figures use different group denominators again, and the record does not explain the difference.

Single-blind describes the masking recorded for the trial, but the identity of the masked party and the practical masking procedures are not reported in the registry record. The allocation method beyond the description “randomized” is also not reported. The record does not report the original sample-size justification, the intended allocation ratio, or whether interim analyses were planned. The planning illustration associated with the posted results is a separate calculation based on the observed effect, not a description of the trial’s original design.

The trial’s primary endpoint concerned symptomatic infection requiring treatment, while its listed additional outcomes broadened the question to culture confirmation, antibiotic resistance, cost-effectiveness, and side effects. The registry record does not include enough detail to establish how each of these outcomes was collected or analyzed. The record lists seven outcome measures and one analysis, but the full statistical analysis plan is not reported.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent to Treat model

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Treatment of Clinically Suspected UTI - Using Intent to Treat Analysis, measured over 3 weeks post-operative.

The primary endpoint counts participants with a clinically suspected UTI requiring antibiotic treatment, assessed at 3 weeks post-operative. The registry defines a qualifying case as at least two listed symptoms in the absence of vaginal symptoms: urinary frequency, urinary urgency, dysuria, fever over 38oC/100.4oF, suprapubic, flank, or back pain, and/or chills. The primary analysis is identified as intent to treat.

This endpoint focuses on symptomatic illness that led to treatment rather than on a positive urine culture alone. That distinction is relevant because symptoms and culture results represent different aspects of infection: a participant may meet the clinical definition without a positive culture, and a positive culture does not by itself establish that the clinical endpoint was met. Culture-positive symptomatic UTI was listed as a secondary outcome.

Using a clinically defined endpoint can make a trial’s question relevant to patient experience and treatment decisions, while requiring consistent symptom assessment and treatment criteria. The record does not report how symptom information was gathered, how treatment decisions were standardized across groups, or how ambiguous cases were adjudicated. The stated timeframe is 3 weeks post-operative; although the trial summary discusses prevention after catheter removal, the endpoint entry does not specify the timing of assessment relative to catheter removal.

7. Results Posted in the Registry

• Ciprofloxacin: 12.9% (12/93) versus 12.9% (13/101) on control; risk difference 0.0 percentage points (95% CI -9.4 to 9.5), risk ratio 1.00 (0.48–2.09); unadjusted two-proportion z-test p = 0.995.

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 Culture-positive Symptomatic UTI

• 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:
  • Ciprofloxacin: 4.3% (4/93) versus 5.0% (5/101) on control; risk difference -0.6 percentage points (95% CI -6.6 to 5.3), risk ratio 0.87 (0.24–3.14); unadjusted two-proportion z-test p = 0.830.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ciprofloxacin and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists additional questions about culture-positive symptomatic UTI, antibiotic resistance, cost-effectiveness, and side effects. Among the secondary outcome results detailed in the record summarized for this comparison, culture-positive symptomatic UTI has a posted numerical comparison. Numerical results for antibiotic resistance and cost-effectiveness are not reported in the registry record. The safety listing gives adverse-event counts, but the record does not supply the broader detail needed to interpret side-effect prevalence fully.

At a broad level, the culture-positive outcome does not suggest a clearly separated group pattern in the posted summary, which is consistent with the primary result’s near-zero point estimate. The outcomes are related but not identical: the primary endpoint is clinically suspected UTI requiring treatment, whereas the culture-positive endpoint adds microbiological confirmation. Agreement in broad pattern does not make the endpoints interchangeable, and neither result resolves the uncertainty in the primary comparison.

Secondary outcomes are generally less decisive when they are assessed alongside a primary endpoint without a reported multiplicity plan. Examining many outcomes creates more opportunities for chance findings. An unadjusted p-value for a secondary comparison does not account for the number of questions considered, so it should be interpreted as exploratory rather than as independent confirmatory evidence. The registry record does not report whether adjustment for multiple comparisons was planned or performed.

The record identifies four secondary outcomes as posted, but does not provide a full account of methods and results for each of the listed topics. Absence of a numerical result in the record should not be interpreted as a zero effect or as evidence that no event occurred. It means that the relevant result is not reported in the registry record. Separate reporting would be needed to judge the consistency, precision, and clinical relevance of those outcomes.

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

• Number of Participants With Culture-positive Symptomatic UTI
• Antibiotic Resistance of Culture-positive Symptomatic UTI
• Cost-effectiveness of Prophylaxis With Methenamine Hippurate for Prevention of Post-operative UTI Compared to Prophylaxis With Fluoroquinolones
• Prevalence of Side Effects

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a binary outcome: each participant either met the endpoint definition or did not. The posted group counts therefore describe participants with an event, rather than a continuous measurement such as a laboratory value. A risk is the proportion of participants in a group who experienced the event. The registry’s posted group counts and denominators allow an unadjusted comparison of those risks.

What does the risk difference express?

The risk difference subtracts one group’s event risk from the other’s. In this comparison the calculation is oriented as ciprofloxacin minus methenamine, so a positive estimate indicates a higher estimated event risk in the ciprofloxacin group, and a negative estimate indicates a lower estimated event risk in that group. The estimated risk difference is < 0.001. This is a comparison of absolute risks, rather than a ratio of risks. It is useful for describing the size and direction of the observed contrast on the risk scale.

How do ratios differ from a risk difference?

A risk ratio compares one group’s risk with the other group’s risk by division. An odds ratio compares the odds of an event between groups; odds are not the same as risks, especially when events are not rare. The recalculated risk ratio is 1.002, with a 95% confidence interval from 0.482 to 2.085. The recalculated odds ratio is 1.003, with a 95% confidence interval from 0.433 to 2.324. These are alternative scales for describing the comparison, not separate trial outcomes. Each estimate has its own interpretation and uncertainty. The registry’s sponsor-reported non-inferiority entry is a separate analysis and should not be conflated with these recalculations.

What does the p-value say?

The unadjusted p-value for the recalculated primary risk difference is 0.995. A p-value measures how compatible the observed data are with a specified null model, under the assumptions of the test. It does not quantify the chance that the null model is true, and it does not measure the size or importance of an effect. A large p-value does not prove equivalence or non-inferiority. Such conclusions require an appropriate design, a prespecified margin where relevant, and an analysis that addresses the intended question. The non-inferiority margin and full sponsor analysis details are not reported in the registry record.

Why can a binary outcome comparison be imprecise?

Precision depends in part on the amount of information in the data. For a binary endpoint, the number of participants who experience the event contributes directly to how well the event risks can be estimated. When events are limited, estimates may vary substantially across plausible underlying event rates. A confidence interval makes that uncertainty visible. It is therefore possible to observe a point estimate close to zero while retaining considerable uncertainty about the true difference.

The recalculated estimates are described as unadjusted because they use the posted summary statistics without adjustment for other variables. An adjusted model could account for prespecified covariates, but whether one was planned or performed is not reported in the registry record. The listed primary population is intent to treat, but details about exclusions, missing outcomes, and the exact implementation of that population are not reported.

General statistical context: a randomized comparison is intended to make the groups comparable on average, but randomization does not guarantee exact balance in every characteristic, particularly in a finite trial. The registry does not report baseline characteristics in the registry record for this comparison, so no statement about balance can be made. Likewise, the posted summary counts do not permit assessment of outcome timing, adherence, or participant-level patterns.

The planning calculations are illustrations based on the observed effect and stated assumptions, not the trial’s original design calculations. They do not revise the observed result or supply evidence that the study had a particular level of power. Their purpose is to show how a hypothetical future design’s required group size would vary with the effect size chosen for detection.

11. Confidence Intervals and Precision

The recalculated primary risk difference is < 0.001, with a 95% confidence interval from -0.094 to 0.095. The interval includes zero, which corresponds to no difference on the risk-difference scale, and extends to estimates in either direction. Its width indicates that the posted data do not determine the comparative risk with high precision. The point estimate alone should not be read as an exact or definitive difference.

A confidence interval is a range generated by a statistical procedure that, under its assumptions, is designed to cover the true effect at the stated rate over repeated applications. It is not a range containing a specified probability that the true effect lies within these particular limits. The interval also does not identify which values would be clinically important. The registry record does not report a clinical threshold for interpreting the risk difference.

For the ratio measures, the recalculated risk ratio is 1.002, with a 95% confidence interval from 0.482 to 2.085; the recalculated odds ratio is 1.003, with a 95% confidence interval from 0.433 to 2.324. These intervals also encompass values corresponding to no difference and allow effects in either direction. The risk-difference interval and ratio intervals use different scales, so their numerical limits should not be compared directly.

The event counts and group denominators are modest relative to the very large planning illustrations based on the observed effect. That does not establish what sample size the original trial should have used: the original design assumptions and target effect are not reported in the registry record. The practical interpretation is that the posted estimates leave substantial uncertainty, rather than that either regimen has been shown to be equivalent or different.

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, not total participants, for the binary outcomes in this analysis. They are illustrations computed from the observed effect, using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the hypothetical number of participants per arm needed for a future study to have an 80% chance of detecting the chosen effect under the stated assumptions, if that effect were the true one and the analysis assumptions held. The 90% power column uses a higher target chance of detecting that effect and therefore requires more participants per arm. These are design-planning quantities, not estimates of what happened in the completed trial.

The rows illustrate planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants. Since the observed primary effect is close to zero, calculations based on fractions of that effect produce extremely large planning figures. They should not be treated as a recommendation for a future study without specifying a scientifically meaningful target effect and considering the intended design.

This is not observed power. It is a planning illustration conditional on the stated assumptions and the effect size chosen for detection. The original rationale for the trial’s enrollment and any planned power calculation are not reported in the registry record. The figures do not change the interpretation of the observed confidence interval or establish that the completed trial was designed to detect a particular effect.

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 = 0.129; treatment proportion p₁ = 0.129; average p̄ = 0.129.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4738 = 0.9287.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4738 = 0.3988.
4. n = (0.9287 + 0.3988)² / (0.0003)² = 17,276,109.1, rounded up to 17,276,110 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 <- 0.128712871287129                          # control proportion
p1 <- 0.129032258064516                          # 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(2358993)
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 = 17,276,110 (80% power), 23,127,809 (90% power)
 75% of observed effect: n per arm = 30,704,977 (80% power), 41,105,252 (90% power)
 50% of observed effect: n per arm = 69,067,955 (80% power), 92,462,395 (90% power)
power.prop.test: 17276109 
Simulated power at n = 17,276,110 per arm: 0.796 (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 includes a sponsor-reported non-inferiority analysis for the primary outcome. Its reported measure is a risk ratio recorded as “-.01,” with a 95% confidence level indicated, but no confidence limits, p-value, or analysis method are reported. The entry therefore supplies less information than would be needed to assess the non-inferiority claim independently. In particular, the non-inferiority margin and the decision rule are not reported in the registry record.

The recalculated result is a simple unadjusted comparison from the posted group counts. It gives a risk difference of < 0.001 and a 95% confidence interval from -0.094 to 0.095. That calculation is not a reconstruction of the sponsor’s full analysis: the reported sponsor measure is different, and the sponsor’s method is not specified. The two entries should be read as distinct analyses rather than as interchangeable estimates.

The record marks discrepancy as false, so no disagreement is flagged between the posted summary and the sponsor analysis. That does not fill in the missing methodological details or make the non-inferiority analysis reproducible from the available entry. The recalculation describes what follows from the posted counts under an unadjusted comparison; the registry’s sponsor-reported analysis remains the trial’s own reported non-inferiority result, with its supporting details not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry names a primary endpoint and several additional outcomes, but a complete statistical analysis plan is not reported in the registry record. It is therefore not possible to determine whether the outcome hierarchy, analysis methods, or decision thresholds were fixed before results were examined. The record also does not report whether interim analyses were planned or conducted.

Multiplicity arises when several outcomes or comparisons are tested. Even if each test uses a conventional threshold, considering multiple tests increases the chance that at least one result will appear noteworthy by chance. The recalculated p-values are unadjusted. The registry does not report a multiplicity adjustment or a prespecified strategy for interpreting the secondary outcomes. Consequently, unadjusted secondary findings should carry less confirmatory weight than a prespecified primary analysis.

The primary population is described as intent to treat. That label generally refers to analyzing participants according to randomized assignment, but the registry does not report how this was implemented for participants without outcome data, those who withdrew, or those who did not follow the assigned regimen. The primary outcome denominators are 101 and 93, while overall enrollment is 201. The registry record does not explain the difference or state whether every randomized participant had an evaluable primary outcome.

Missing outcome data can affect a binary comparison if the probability of missingness differs between groups or is related to the outcome. The record does not report the number of missing primary outcomes, reasons for missingness, imputation methods, or sensitivity analyses. It is therefore not possible to assess how missing data were handled or whether alternative assumptions would change the result.

The sponsor’s non-inferiority entry does not report its margin, method, confidence limits, or p-value. These omissions limit assessment of the non-inferiority analysis. The registry record also does not report adjustment for baseline characteristics, subgroup analyses, or a complete analysis population definition. These absences do not establish that such procedures were not undertaken; they mean that they are not reported in the registry record.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports no serious adverse events in either safety group: 0 of 103 for methenamine and 0 of 94 for ciprofloxacin. It also reports no deaths in either group. For other adverse events, the record lists 0 of 103 in the methenamine group and 3 of 94 in the ciprofloxacin group. These figures describe the counts recorded in the registry; they do not establish that no unrecorded events occurred.

The safety denominators differ from the primary efficacy denominators. The registry does not report why those populations differ, how adverse events were defined or collected, or how long safety follow-up lasted. No serious adverse-event terms are listed. Without further detail, the other adverse events cannot be characterized by type, severity, timing, or relationship to treatment.

Zero observed serious events in these groups is not proof that serious harms are impossible or that the treatments have identical safety profiles. Rare events may not appear in a trial of this size, and comparisons based on small event counts are imprecise. The posted safety figures should be interpreted as descriptive counts within the registry’s reported follow-up, not as a comprehensive safety assessment.

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

The posted primary data show similar observed counts of participants meeting the treatment-based UTI definition in the two randomized groups. The unadjusted risk-difference estimate is close to zero, but its confidence interval is broad and includes differences in both directions. The result therefore offers limited precision about the comparative event rates. It does not establish that the regimens are identical, nor does it establish that one is superior.

The registry includes a non-inferiority analysis, but its entry lacks the margin and statistical details needed to assess the claim. The unadjusted recalculation is not a substitute for that analysis. It is a separate summary-statistic comparison and should be interpreted on its own terms.

The findings concern the recorded population of patients requiring short-term catheterization after pelvic reconstructive surgery, the trial’s treatment schedules, and its stated postoperative timeframe. The result does not automatically extend to other patient populations, procedures, catheter practices, or durations of treatment. Details needed to evaluate those differences are not reported in the registry record.

The primary outcome measures clinically suspected infection requiring antibiotics. It does not answer every question about culture confirmation, resistance, cost-effectiveness, or adverse effects. The registry lists those additional topics, but complete results and methods are not reported for each. Nor do the posted counts establish what would happen to an individual patient. They are group-level trial results and do not provide medical advice.

The most defensible conclusion is statistical rather than prescriptive: the observed point estimate is near no difference, while the uncertainty remains substantial. Further interpretation would require fuller reporting of the analysis plan, the non-inferiority margin, missing-data handling, and the additional outcome results.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its precision need to be read together. A comparison can produce an estimate close to no difference while still allowing meaningful effects in either direction. Looking only at the point estimate or an unadjusted p-value would conceal the uncertainty conveyed by the confidence interval.

It also illustrates the distinction between superiority and non-inferiority questions. A conventional test for a difference and a non-inferiority analysis answer different questions. Non-inferiority requires a justified margin and a decision procedure designed for that purpose; a non-significant difference alone does not demonstrate non-inferiority. The registry’s abbreviated sponsor analysis makes clear why reporting the margin and interval is important.

The comparison also highlights the role of outcome definition. A treatment-based clinical endpoint and a culture-confirmed endpoint capture related but distinct events. Clear definitions and complete reporting help readers understand what the measured outcome represents, how it relates to the clinical question, and whether conclusions hold across outcomes.

Finally, the planning illustration shows how a small observed effect can yield very large sample-size requirements when the same effect or a smaller fraction is targeted. Those calculations are not a verdict on the original design, whose assumptions are not reported. They demonstrate that prospective planning depends on choosing a meaningful effect and stating assumptions clearly, rather than treating the observed result as a definitive design target.

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 leaves important design and analysis details unreported. It does not give the original sample-size justification, allocation procedures beyond randomization, identity of the masked party, full analysis plan, or any interim-analysis plan. These omissions constrain assessment of how the trial was designed and how the reported analyses relate to prespecified objectives.

The primary efficacy denominators do not account for the overall enrollment figure in the record, and the safety denominators differ from the efficacy denominators. Reasons for these differences and details about the randomized population are not reported. The registry also does not describe missing outcomes, withdrawals, adherence, or the handling of participants with incomplete follow-up. These gaps make it difficult to evaluate the intent-to-treat implementation and potential missing-data bias.

The primary comparison is available as summary counts, so the recalculation is unadjusted and cannot examine participant-level covariates or assess alternative model specifications. The record does not report baseline characteristics in the registry record for the comparison. The confidence interval is broad, limiting precision, and the sponsor’s non-inferiority entry lacks the margin and supporting statistics needed for independent assessment.

Additional limitations concern outcome and safety reporting. The registry does not explain how symptoms and treatment decisions were assessed, how culture results were collected, or how adverse events were defined and followed. Numerical results and methods for some listed secondary topics are not reported in the registry record. These limitations should be distinguished from evidence that an outcome was absent: lack of a posted result does not mean that no events or effects occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Short-course Methenamine Hippurate for Prevention of Post-operative UTI — NCT02358993.
• Registry record last updated 2022-02-25; status last verified 2022-02.
• Results first posted 2022-02-25.
• 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

The registry describes a completed, randomized, single-blind, parallel-group trial of methenamine hippurate compared with ciprofloxacin for prevention of post-operative UTI among patients requiring short-term catheterization after pelvic reconstructive surgery. The record lists enrollment of 201 and a primary outcome of clinically suspected UTI requiring antibiotic treatment within 3 weeks post-operative.

The primary summary counts are 13 of 101 participants for methenamine and 12 of 93 for ciprofloxacin. The unadjusted recalculated risk difference is < 0.001, with a 95% confidence interval from -0.094 to 0.095. The interval indicates substantial uncertainty about the size and direction of the comparative effect.

The registry also lists a sponsor-reported non-inferiority analysis, but its margin and supporting statistical details are not reported. Additional outcomes include culture-positive symptomatic UTI, resistance, cost-effectiveness, and side effects; complete results and methods for these topics are not all reported in the registry record.