Oral Sulopenem-etzadroxil/Probenecid Versus Ciprofloxacin for Uncomplicated Urinary Tract Infection in Adult Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral Sulopenem-etzadroxil/Probenecid Versus Ciprofloxacin for Uncomplicated Urinary Tract Infection in Adult Women (NCT03354598), a randomized phase 3 study. The primary outcome is Percentage of Microbiologic Modified Intent to Treat Resistant (Micro-MITTR) Participants With Overall Success.

2. Clinical Question

3. Trial Design

This was a prospective, Phase 3, randomized, multicenter, double-blind study with a parallel-group design. The registry record describes masking as quadruple. It does not identify in this record which particular groups or roles were masked, so the label should not be taken to specify those details. Random allocation and the parallel model indicate that participants were assigned to one of the two treatment arms for comparison.

The study compared oral sulopenem-etzadroxil/probenecid with oral ciprofloxacin in adult women with uncomplicated urinary tract infection. The recorded sulopenem-etzadroxil/probenecid regimen was 500 mg twice daily for 5 days; the ciprofloxacin regimen was 250 mg twice daily for 3 days. The registry record reports enrollment of 1671 participants. The primary outcome, however, was evaluated in the narrower microbiologic modified intent-to-treat resistant population, comprising participants whose baseline uropathogen was not susceptible to ciprofloxacin.

The study began on 2018-08-01, had a primary completion date of 2020-01-16, and is listed as completed. These dates describe the registry record and do not by themselves establish when each participant was followed or when each analysis was performed. The primary outcome timeframe is Day 12+/-1 day.

Four outcome measures are recorded. One secondary outcome is named: microbiologic success in the same resistant microbiologic modified intent-to-treat population. The registry record does not report the original sample-size justification, the full statistical analysis plan, planned interim analyses, or the details of the randomization procedure. The posted planning illustrations are based on observed effects and are not evidence of the trial's original design assumptions.

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: micro-MITTR population: patients with baseline uropathogen non-susceptible to the comparator ciprofloxacin.

5. Baseline Characteristics

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

Population: Intent to Treat (ITT) Participants

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Microbiologic Modified Intent to Treat Resistant (Micro-MITTR) Participants With Overall Success, measured over Day 12+/-1 day.

The primary endpoint is the percentage of participants in the microbiologic modified intent-to-treat resistant population with overall success at Day 12+/-1 day. This population is defined by a baseline uropathogen that was non-susceptible to ciprofloxacin. For an individual participant to count as an overall success, the participant had to meet both components: clinical success, meaning resolution of symptoms present at study entry with no new symptoms, and microbiologic success, meaning eradication of the baseline pathogen.

A combined endpoint can reflect more than one dimension of an outcome. In this case, symptom status and microbiologic findings both contribute to the success classification. A participant who meets only one component does not meet the stated definition of overall success. This makes the endpoint more demanding than either symptom improvement or microbiologic eradication considered on its own, while also making it important to understand precisely how both components were defined.

The endpoint is reported as a percentage of participants with an event, where the event is overall success. It is assessed at a specified follow-up timeframe, rather than as a time-to-event outcome. The registry record identifies the population, composite definition, and timeframe, but does not report further operational details about how symptoms or microbiologic eradication were assessed, adjudicated, or handled when data were unavailable.

Because the endpoint is restricted to participants with baseline pathogens non-susceptible to ciprofloxacin, its interpretation is specific to that resistant subgroup. It should not be generalized automatically to every enrolled participant or to populations defined differently.

7. Results Posted in the Registry

• Ciprofloxacin: 36.0% (50/139) versus 62.6% (92/147) on control; risk difference -26.6 percentage points (95% CI -37.8 to -15.4), risk ratio 0.57 (0.45–0.74); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Microbiologic Modified Intent to Treat Resistant (Micro-MITTR) Patients With Microbiologic Success

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ciprofloxacin: 49.6% (69/139) versus 74.1% (109/147) on control; risk difference -24.5 percentage points (95% CI -35.4 to -13.6), risk ratio 0.67 (0.55–0.81); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Ciprofloxacin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record names one secondary endpoint: microbiologic success in the resistant microbiologic modified intent-to-treat population at Day 12+/-1 day. Its pattern is directionally consistent with the primary overall-success result. That consistency offers context because microbiologic success is one component of the primary endpoint, while the primary endpoint additionally requires clinical success. It should not be treated as an independent replication of the primary finding, since the endpoints concern the same population and share a component.

The secondary outcome helps distinguish the combined outcome from its microbiologic component. A similar direction across these measures indicates that the primary pattern is not confined to the combined classification alone; however, the endpoint definitions and analysis populations remain important. The registry record does not report a detailed statistical analysis plan that would show whether this secondary endpoint was prespecified in a hierarchy or how its analysis related to the primary test.

The secondary comparison is unadjusted. In general, testing multiple outcomes increases the chance that at least one comparison appears notable by chance if each is interpreted without accounting for the testing strategy. An unadjusted secondary result therefore carries less confirmatory weight than a primary result designated for the main question. The size and direction of a secondary estimate can still be informative, but its evidential role depends on prespecification, multiplicity control, missing-data handling, and how many analyses were considered. Those details are not reported in the registry record.

The record lists four outcome measures overall, while one secondary outcome is named in the posted information summarized for this analysis. It does not report a complete account of all planned and conducted secondary analyses. For that reason, the secondary result is best regarded as supportive descriptive context rather than a separate basis for a definitive conclusion. It complements the primary endpoint but does not alter the population or the dual clinical-and-microbiologic definition used for the main outcome.

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

• Percentage of Microbiologic Modified Intent to Treat Resistant (Micro-MITTR) Patients With Microbiologic Success

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the definition of overall success or does not. The displayed percentage is the proportion classified as having the event, where the event is success. A risk difference compares the two arm-specific proportions by subtraction; its sign depends on which arm is subtracted from which. For the posted comparison, a negative risk difference is consistent with a lower success proportion in ciprofloxacin than in sulopenem-etzadroxil/probenecid. This is a general explanation of the measure; it does not change the trial's endpoint definition.

What does the risk difference describe?

As a general statistical concept, a risk difference is an absolute contrast between proportions. It uses the original probability scale, so it can be read as a difference in the frequency of the event between groups. In a trial report, the order of the groups matters: reversing the subtraction reverses the sign, even though the underlying comparison is unchanged. The registry record posts a risk difference, a confidence interval, and an unadjusted p-value for the comparison. Those are complementary summaries: the estimate gives the direction and magnitude on the proportion scale, the interval communicates uncertainty, and the p-value assesses compatibility with a null comparison under the analysis assumptions.

What does a confidence interval add?

In general, a confidence interval is an interval estimate that reflects sampling uncertainty under a specified method. A narrower interval indicates greater precision on the scale being estimated; a wider interval indicates less precision. It does not include every source of uncertainty: it cannot correct a poorly defined outcome, selection into the analysis population, missing data, or bias in measurement. Nor should an interval be interpreted as a guarantee that the true value lies within its limits. For this comparison, the posted interval for the risk difference is entirely below zero, while the exact interval bounds are best read in the posted results rather than restated.

How should the p-value be read?

The primary comparison reports p < 0.001 without an adjustment stated in the registry record. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an observed contrast. It also does not convey precision as directly as the confidence interval. The result should therefore be read together with the arm percentages, the risk-difference estimate, its interval, and the endpoint's population and definition.

Why distinguish the population from enrollment?

The total enrollment is 1671, whereas the primary analysis population is defined by baseline pathogen non-susceptibility to ciprofloxacin and has arm denominators of 147 and 139. This distinction matters because the target population for the primary contrast is the resistant subgroup, not all randomized participants. As a general principle, an analysis restricted by a baseline characteristic may address a clinically and biologically specific question, but its findings apply most directly to people meeting that characteristic. The registry record does not report all details needed to assess the analysis population's construction, such as the full participant flow or handling of missing baseline microbiology.

Why can over-dispersion matter?

Over-dispersion is a general concern when observed variation is greater than a model assumes. If a method assumes that observations vary according to a particular probability model but the data are more variable, standard errors may be too small and confidence intervals too narrow. For a binary outcome, the choice of model and any clustering or dependence among observations can affect uncertainty estimates. The registry record does not provide enough detail to determine whether over-dispersion or clustering was relevant or how either was handled. This is a general methodological consideration, not a claim that the trial results exhibit over-dispersion.

The registry record reports no formal analyses under its count of analyses, although it includes posted arm outcomes and comparisons. The detailed statistical model, covariate adjustment, missing-data approach, and multiplicity procedure are not reported in the registry record. Therefore, the safest reading is to describe the posted, unadjusted summaries without attributing an unreported model or analysis strategy to the investigators.

11. Confidence Intervals and Precision

Precision is reflected most directly by the confidence interval around the risk-difference estimate. The primary comparison's interval lies below zero, indicating that the posted interval does not include a null risk difference under the method used. The interval nevertheless spans a range of possible contrasts, so the point estimate should not be treated as exact. The endpoints of the interval are available in the posted results; the important interpretive point is that the interval communicates uncertainty around the estimated comparison, not certainty about a single value.

The primary arm denominators are 147 and 139. These are the numbers contributing to the displayed primary outcome, not the overall enrollment of 1671. In general, fewer observations tend to produce less precise estimates, although precision also depends on the observed proportions and analysis method. The interval should therefore be considered alongside the subgroup definition and the arm-specific percentages, rather than as an abstract measure separated from the trial population.

A confidence interval is not a probability statement about the true effect after the data have been observed. In general, it describes the range of parameter values that would be compatible with the data under a repeated-sampling procedure and the method's assumptions. It does not account automatically for bias, missing outcomes, limitations in outcome measurement, or selective reporting. The registry record does not report all the methods needed to assess those issues.

The primary comparison also has an unadjusted p-value of <0.001. A small p-value and a confidence interval that excludes zero are related ways of conveying evidence against a null risk difference, but neither alone answers questions about relevance, applicability, or the reliability of unreported design and analysis details. The width and location of the interval, together with the definition of overall success, are central to judging how precisely the posted data distinguish between the arms.

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 estimates are planning illustrations calculated from the observed effect, not the trial's original sample-size design. For these binary outcomes, the estimates are participants per arm. They are not total event counts. The rows consider planning for 100%, 75%, and 50% of the observed effect, and the columns describe participants per arm for 80% power and participants per arm for 90% power.

In general, power is the probability that a planned study will detect an effect of a specified size under its assumptions, if that effect is present. The 80% column means the estimated per-arm sample size for a design with an 80% chance of detecting the assumed effect; the 90% column uses a higher target chance of detection. These are planning targets, not guarantees about the result of a future study. The posted illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect.

Smaller effects are harder to distinguish from random variation and generally require more participants to achieve the same planned power. Thus, the rows for smaller fractions of the observed effect call for larger per-arm samples than planning around the full observed effect. These calculations are sensitive to their assumptions, including the effect chosen for planning; an observed effect can differ from the effect that would be expected in a new study.

This is not observed power. It is a planning illustration based on the observed effect, and it does not recover the original justification for enrollment. The trial's original sample-size assumptions are not reported in the registry record. Time-to-event sample-size illustrations, when present, are expressed as total events, but the estimates discussed for these binary outcomes are participants per arm.

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 = 0.626; treatment proportion p₁ = 0.360; average p̄ = 0.493.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3858.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6815 = 0.5736.
4. n = (1.3858 + 0.5736)² / (-0.2661)² = 54.2, rounded up to 55 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 <- 0.625850340136054                          # control proportion
p1 <- 0.359712230215827                          # 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(3354598)
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 = 55 (80% power), 73 (90% power)
 75% of observed effect: n per arm = 98 (80% power), 130 (90% power)
 50% of observed effect: n per arm = 218 (80% power), 291 (90% power)
power.prop.test: 54.2 
Simulated power at n = 55 per arm: 0.802 (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 evaluates more than one outcome, comparison, subgroup, or analysis. In general, the more statistical tests that are conducted, the greater the chance of obtaining at least one apparently notable result by chance if all tests are treated as independent opportunities for confirmation. A prespecified testing hierarchy or a suitable adjustment can address this issue, but the registry record does not report whether either was used. The posted primary and secondary p-values are unadjusted, so they should not be interpreted as if a multiplicity correction had been applied.

The registry record identifies the primary endpoint and one secondary endpoint, and it reports four outcome measures. It does not provide a full statistical analysis plan, a complete account of planned hypotheses, or a multiplicity strategy. The relationship between the reported outcomes and any other planned analyses is therefore not reported in the registry record. This limits assessment of how strongly the secondary result should be treated as confirmatory and whether the primary result was selected from a broader set of analyses.

Missing data can affect both the numerator and denominator of a percentage outcome. In general, excluding participants without an evaluable outcome can bias a comparison if the chance of missingness differs between groups or is related to the outcome. Other approaches may make different assumptions about missing values. The registry record does not report the amount or pattern of missing primary outcome data, the rules used to classify participants without complete information, or sensitivity analyses addressing missingness.

The primary analysis population is defined by baseline pathogen non-susceptibility to ciprofloxacin. The record gives arm denominators for that outcome, but does not report a complete participant flow or all details of how participants were included in the analysis. The original sample-size justification, planned interim analyses, and detailed statistical plan are also not reported in the registry record. These omissions do not invalidate the posted summaries, but they constrain independent assessment of the analysis choices and the extent to which the results reflect the prespecified plan.

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: diarrhoea (0.1%), bile duct stone (0.1%), pneumonia (0.1%), abdominal pain upper (0.1%), small intestine obstruction (0.1%).

The registry record reports serious adverse events among 833 participants at risk in the sulopenem-etzadroxil/probenecid group and 827 at risk in the ciprofloxacin group. Serious adverse events were recorded for 6 participants in the sulopenem-etzadroxil/probenecid group and 2 in the ciprofloxacin group. The record also reports other, non-serious adverse events for 103 and 21 participants, respectively. These counts describe the recorded safety summaries; they are not adjusted comparisons and do not establish that treatment caused an event.

Deaths are reported as 1 in the sulopenem-etzadroxil/probenecid group and 0 in the ciprofloxacin group. The serious-event terms listed include Diarrhoea, Bile duct stone, Pneumonia, Abdominal pain upper, small intestine obstruction, and chest pain, each reported as 0.1%. The registry record does not provide detailed event narratives or information that would support attributing these events to a treatment.

Serious adverse events and other adverse events are separate categories in the record. Counts should be read with their at-risk denominators and with the distinction between seriousness and event frequency in mind. The listed figures do not by themselves establish a comparative safety profile, and they are not a substitute for detailed assessment of event definitions, timing, severity, or relatedness, which are not reported in the registry record.

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

The posted primary result describes overall success at Day 12+/-1 day among participants whose baseline uropathogen was non-susceptible to ciprofloxacin. The outcome requires both resolution of study-entry symptoms without new symptoms and eradication of the baseline pathogen. The observed arm percentages differ, and the unadjusted comparison reports p < 0.001. The risk-difference interval is entirely below zero under the posted comparison's ordering.

These data do not mean that every participant in one group achieved success or that every participant in the other group did not. The percentages summarize group-level outcomes. They also do not show which individual participants met only the clinical component, only the microbiologic component, or neither, because those component-level counts are not reported in the registry record.

The primary result applies most directly to the resistant microbiologic modified intent-to-treat population, not automatically to all adult women with uncomplicated urinary tract infection or to all participants enrolled. The registry record does not report enough detail to assess how outcomes might differ in participants whose pathogens were susceptible to ciprofloxacin, in other populations, or at a different follow-up time. It also does not provide the full analysis plan or the handling of missing outcomes.

A statistically notable unadjusted comparison does not, by itself, establish clinical importance, generalizability, or causation for each reported adverse event. Confidence intervals communicate sampling uncertainty but do not remove potential bias or uncertainty arising from unreported methods. The secondary microbiologic endpoint provides related context, but its unadjusted status and overlap with the primary endpoint limit its independent confirmatory force.

The trial record supports a description of the observed results under the recorded regimens, endpoint definition, population, and timeframe. It does not justify a treatment recommendation. Interpretation beyond those conditions requires evidence and details not reported in the registry record.

17. Why This Trial Matters Statistically

Several statistical features make this trial useful to examine. It is a randomized, parallel-group Phase 3 study with a binary primary outcome and a clearly stated composite definition. The primary result concerns a defined resistant subgroup, making the relationship between the overall enrollment and the endpoint-specific denominators especially important. Readers can distinguish the broad trial population from the population that contributes to the main comparison.

The endpoint requires success on both a clinical and a microbiologic component. This illustrates how a composite can combine outcomes that are related but not identical, and why interpretation depends on knowing exactly what qualifies as success. The secondary microbiologic outcome can be read as context for one component, while the primary result retains the broader combined definition.

The posted comparison includes arm percentages, a risk difference, a confidence interval, and an unadjusted p-value. Considering these measures together helps separate the observed proportions from the estimated absolute contrast, and the contrast's uncertainty from a test of a null hypothesis. The sample-size illustrations also offer a teaching example of how planning estimates depend on the effect chosen and on assumptions about allocation, significance level, and approximation.

At the same time, the record demonstrates why statistical interpretation requires attention to what is not reported. The original sample-size justification, detailed analysis plan, multiplicity approach, missing-data methods, and interim-analysis plans are not reported in the registry record. Recognizing those limits helps prevent unadjusted results and planning illustrations from being mistaken for a complete account of the trial's design and analysis.

18. Limitations

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

The primary outcome is restricted to participants with a baseline pathogen non-susceptible to ciprofloxacin. The result therefore has a narrower target population than the full adult-women population described for the study. The registry record does not report enough detail about screening, participant flow, or baseline microbiology to assess how the resistant subgroup was assembled beyond its stated definition.

The endpoint combines clinical symptom resolution and microbiologic eradication. This is informative as a joint outcome, but the registry record does not provide the separate component results in the information summarized for this analysis. It is therefore not possible to use the primary percentage alone to determine how much each component contributed to the overall-success pattern.

The record does not report the original sample-size justification, full statistical analysis plan, handling of missing outcome data, multiplicity adjustment, or interim-analysis plans. It also does not give further operational details about outcome assessment, masking roles, or the randomization procedure. These omissions limit assessment of the prespecification and robustness of the posted results.

The posted p-values are unadjusted, and the secondary outcome is related to the primary endpoint. The record does not report a full accounting of planned and conducted analyses, so the extent of multiplicity cannot be assessed. The sample-size estimates are planning illustrations based on observed effects, not a substitute for the original design rationale. Safety summaries provide event counts and selected terms, but the record does not report detailed narratives or event attribution in the registry record.

These limitations are specific to the registry information available for this trial. They do not establish that an unreported procedure was or was not conducted; they indicate that the registry record does not report the detail needed to evaluate it.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Oral Sulopenem-etzadroxil/Probenecid Versus Ciprofloxacin for Uncomplicated Urinary Tract Infection in Adult Women — NCT03354598.
• Registry record last updated 2021-01-12; status last verified 2019-12.
• Results first posted 2020-12-17.
• 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

NCT03354598 is a completed, randomized, quadruple-masked, parallel Phase 3 trial sponsored by Iterum Therapeutics, International Limited. It enrolled 1671 participants and compared oral sulopenem-etzadroxil/probenecid with oral ciprofloxacin in adult women with uncomplicated urinary tract infection.

The primary endpoint was overall success at Day 12+/-1 day in the microbiologic modified intent-to-treat resistant population. Success required both clinical symptom resolution without new symptoms and eradication of the baseline pathogen. The registry record reports arm-specific percentages and an unadjusted comparison for this population. One secondary endpoint addresses microbiologic success in the same population.

The record lists four outcome measures, but does not report the original sample-size justification, detailed statistical analysis plan, multiplicity strategy, missing-data methods, or interim-analysis plans. Planning estimates based on observed effects are illustrations rather than the trial's original design assumptions. These details should be kept in view when interpreting the posted efficacy and safety summaries.