Study to Assess the Efficacy, Safety and Pharmacokinetics of Orally Administered Tebipenem Pivoxil Hydrobromide (SPR994) Compared to Intravenous Ertapenem in Participants With Complicated Urinary Tract Infection (cUTI) or Acute Pyelonephritis (AP): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy, Safety and Pharmacokinetics of Orally Administered Tebipenem Pivoxil Hydrobromide (SPR994) Compared to Intravenous Ertapenem in Participants With Complicated Urinary Tract Infection (cUTI) or Acute Pyelonephritis (AP) (NCT03788967), a randomized phase 3 study. The primary outcome is Overall Response (Combined Clinical Cure and Microbiological Eradication) at Test-of-Cure (TOC) in Micro Intent-to-Treat Population.

2. Clinical Question

The clinical question therefore combines two kinds of evidence about the infection. Clinical cure concerns resolution or meaningful improvement of baseline signs and symptoms, without new symptoms that warrant further antimicrobial therapy. Microbiological eradication concerns the urine pathogen result, with a separate repeated blood-culture criterion for participants whose baseline blood culture was positive. A participant counted as an overall responder had to meet both components.

3. Trial Design

The registry describes a completed, randomized, parallel-group Phase 3 study comparing TBPM-PI-HBr with ertapenem in participants with complicated urinary tract infection or acute pyelonephritis. The listed enrollment is 1372. The official title characterizes the study as double-blind and double-dummy, while the registry’s masking classification is quadruple. The record does not specify which roles were masked, so the meaning of that classification for individual study personnel is not reported in the registry record.

The comparison paired an oral regimen with an intravenous regimen. Participants assigned TBPM-PI-HBr received dummy infusion; participants assigned ertapenem received dummy tablets. This double-dummy arrangement makes it possible to compare treatments delivered by different routes while giving each group both an active treatment and a matching placebo treatment. The arm descriptions list TBPM-PI-HBr 600 mg tablets administered orally three times daily up to Day 15, and ertapenem 1 g by intravenous infusion once daily up to Day 14. The TBPM-PI-HBr arm description is truncated in the registry record, so the complete dosing qualifications are not available there.

The primary outcome is assessed at test of cure on Day 19. The stated primary population is Micro-ITT, which the record describes as including randomized participants with a confirmed diagnosis and a positive screening urine culture and/or qualifying positive screening blood culture. The detailed population definition is cut off in the record, so its full eligibility rules are not reported in the registry record. Other listed analyses use populations described as microbiologically evaluable, clinically evaluable, and Micro-ITT, with outcomes assessed at end of treatment, test of cure, and late follow-up.

The registry lists the study as completed and gives its start and primary completion dates, but those dates are not necessary to interpret the comparison. Details of the randomization procedure, allocation concealment, masking roles, site structure, and trial’s original sample-size justification are not reported in the registry record. The registry also does not provide the full protocol or statistical analysis plan in the record summarized for this analysis.

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: Participants with diagnosis of complicated Urinary Tract Infection (cUTI) or Acute Pyelonephritis (AP) were enrolled to receive tebipenem pivoxil hydrobromide (TBPM-PI-HBr) and ertapenem.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Microbiological intent-to-treat population (Micro-ITT) included all randomized participants with a confirmed diagnosis of cUTI or AP and a positive Screening urine culture defined as growth of one or two uropathogens at ≥10\^5 CFU/mL and/or positive Screening blood culture with isolation of one or more uropathogens.

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: Safety population included all randomized participants who received any amount of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Overall Response (Combined Clinical Cure and Microbiological Eradication) at Test-of-Cure (TOC) in Micro Intent-to-Treat Population, measured over Day 19 (TOC).

The primary endpoint is the overall response at test of cure on Day 19 in the Micro-ITT population. It counts participants who achieved both clinical cure and microbiological eradication. The endpoint is binary at the participant level: each participant either meets the combined response definition or does not.

Clinical cure is defined in the record as complete resolution or significant improvement of the signs and symptoms of complicated urinary tract infection or acute pyelonephritis that were present at baseline, with no new symptoms such that further antimicrobial therapy is warranted. Microbiological eradication is defined by a urine-pathogen threshold: the baseline pathogen or pathogens must be reduced to fewer than 10^3 colony forming units per milliliter. If a blood culture was positive for uropathogen growth at baseline, the stated definition also requires a negative repeated blood culture.

Combining these components gives the endpoint a broader focus than either symptom response or culture status alone. A clinical response without the required microbiological result does not satisfy the combined definition, and neither does eradication without clinical cure. Test of cure is the specified assessment time; it is distinct from the end-of-treatment and late-follow-up assessments listed for secondary outcomes.

The Micro-ITT population is intended to focus the primary comparison on randomized participants who meet the record’s infection and culture criteria. The complete operational definition and handling of participants with missing or unevaluable endpoint data are not reported in the registry record. Those details matter because the endpoint depends on both clinical assessment and microbiological information being available and meeting their respective criteria.

7. Results Posted in the Registry

• Ertapenem 1 g: 61.6% (258/419) versus 58.8% (264/449) on control; risk difference 2.8 percentage points (95% CI -3.7 to 9.3), risk ratio 1.05 (0.94–1.17); unadjusted two-proportion z-test p = 0.404.

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.

Overall Response (Combined Clinical Cure Plus Microbiological Eradication) At Test-Of-Cure (TOC) In The Microbiologically Evaluable (ME) - TOC Population

• 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:
  • Ertapenem 1 g: 65.7% (247/376) versus 61.5% (254/413) on control; risk difference 4.2 percentage points (95% CI -2.5 to 10.9), risk ratio 1.07 (0.96–1.19); unadjusted two-proportion z-test p = 0.222.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ertapenem 1 g and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Cure at EOT Days the Clinically Evaluable (CE-EOT) 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:
  • Ertapenem 1 g: 98.7% (665/674) versus 99.4% (673/677) on control; risk difference -0.7 percentage points (95% CI -1.8 to 0.3), risk ratio 0.99 (0.98–1.00); unadjusted two-proportion z-test p = 0.161.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ertapenem 1 g and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Cure at TOC in the CE-TOC 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:
  • Ertapenem 1 g: 96.9% (617/637) versus 95.3% (611/641) on control; risk difference 1.5 percentage points (95% CI -0.6 to 3.7), risk ratio 1.02 (0.99–1.04); unadjusted two-proportion z-test p = 0.156.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ertapenem 1 g and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover related aspects of response at different assessment times and in different analysis populations. The record lists overall response in a Microbiologically Evaluable population, clinical cure in clinically evaluable and Micro-ITT populations, and sustained clinical cure at late follow-up. These analyses broaden the descriptive picture, but they do not all address the same endpoint or the same set of participants as the primary Micro-ITT outcome at test of cure.

For the secondary results with posted arm counts and recalculations, the general pattern does not provide a clearly decisive contrast that overrides the primary result. Some estimates lean toward one group and others toward the other, while the reported uncertainty includes no difference. This is compatible with the primary analysis’s lack of a clear separation, but secondary outcomes should not be used to declare the primary finding confirmed or contradicted. They are distinct analyses, not independent replications of the primary endpoint.

Interpretation is also constrained because the registry lists many outcome measures and analyses, but the full multiplicity plan is not reported in the registry record. When several outcomes, time points, or populations are examined, the chance of finding an apparently notable result by chance can increase if each is interpreted as a standalone test. Unadjusted secondary results therefore carry less weight than a prespecified primary analysis, particularly when no adjustment strategy or hierarchy is available.

The secondary outcomes can still be useful as supporting descriptions, especially when considered for consistency in direction and clinical construct. Here, differences in the population definitions and the distinction between clinical cure, microbiological response, and sustained response require caution. The posted secondary analyses should be treated as exploratory context unless the protocol or statistical analysis plan establishes their inferential role. That role is not reported in the registry record.

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

• Overall Response (Combined Clinical Cure Plus Microbiological Eradication) At Test-Of-Cure (TOC) In The Microbiologically Evaluable (ME) - TOC Population
• Clinical Cure at End-of-Treatment (EOT), TOC, and Sustained Clinical Cure at Late Follow-Up (LFU) Days in the Micro-ITT Populations
• Clinical Cure at EOT Days the Clinically Evaluable (CE-EOT) Populations
• Clinical Cure at TOC in the CE-TOC Populations
• Sustained Clinical Cure at LFU in the CE-LFU Populations
• Clinical Cure at EOT in the ME-EOT Populations
• Clinical Cure at TOC Days in the ME-TOC Populations
• Sustained Clinical Cure at LFU in the ME-LFU Population

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary because it records whether each participant met the combined response definition. For a binary outcome, the group response proportion is the number meeting the endpoint divided by the number in the relevant analysis population. The posted primary counts are 264 of 449 for TBPM-PI-HBr and 258 of 419 for ertapenem. The recalculation compares these proportions using a risk difference, which expresses the difference between the two group proportions on an absolute scale.

What does the risk difference describe?

A risk difference compares the probability of the outcome in one group with the probability in the other. Its sign depends on which group is subtracted from which. The recalculated comparison is oriented as ertapenem minus TBPM-PI-HBr; therefore a positive estimate indicates a larger observed response proportion in the ertapenem group, while a negative estimate would indicate a larger observed response proportion in the TBPM-PI-HBr group. This direction describes the estimate, not a causal conclusion beyond the randomized comparison and its analysis assumptions.

Absolute differences are useful because they keep the comparison on the outcome-probability scale. Other measures, such as a risk ratio or odds ratio, use different scales and can give a different numerical impression. The risk difference is the measure emphasized for the recalculated primary comparison. No adjusted analysis is reported in the registry record’s posted primary result summary, and the recalculation is unadjusted.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the observed data under the statistical method and its assumptions. In general, a wider interval signals less precision, while a narrower interval signals greater precision. An interval that includes zero for a risk difference is compatible with no difference as well as with differences in either direction within the interval. It should not be read as the probability that the true effect lies inside the particular interval.

The recalculated primary interval includes zero, as does the sponsor-reported interval. Those are not necessarily estimates from the same method or estimand. The registry gives the sponsor result as a risk difference with a 95% interval, but does not specify its method in the posted analysis. It is therefore not possible from the registry record alone to reconcile every methodological detail between that analysis and the simple unadjusted recalculation.

How should the p-value be read?

The unadjusted p-value is 0.404. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Its interpretation depends on the test and analysis plan. The sponsor analysis has no p-value listed in the record, and the primary endpoint’s prespecified test details are not reported in the registry record.

Why do populations and assessment times matter?

The primary analysis uses the Micro-ITT population at Day 19. A Micro-ITT population is not automatically identical to every randomized participant or to the Microbiologically Evaluable population. Endpoint counts and proportions can differ when analysis populations have different inclusion rules. The registry also lists clinically evaluable and microbiologically evaluable analyses, along with end-of-treatment and late-follow-up assessments. Those outcomes can be informative, but they do not replace the primary question because their population definitions or assessment times differ.

The record does not report the full analysis-population definitions, the handling of missing endpoint components, or whether any imputation was used. In general, missingness matters when an endpoint requires both clinical and culture data: whether a participant is excluded, treated as a non-responder, or handled through another method can affect the analysis. The specific approach cannot be inferred from the posted counts.

What does non-inferiority require?

A non-inferiority analysis asks whether the data rule out a loss in effect larger than a prespecified acceptable margin. That is different from testing whether two groups have exactly the same outcome. The margin, direction convention, and complete analysis method are not reported in the registry record. The sponsor’s labelled non-inferiority result should therefore be read as the reported analysis, without independently asserting that its criterion was met from the interval alone.

General statistical interpretation also depends on the design and conduct of the study. Randomization supports a fair comparison in expectation, while masking can reduce some forms of assessment or behavior bias. The registry identifies randomization and masking, but does not report enough procedural detail to evaluate concealment, masking success, or departures from assignment. These limitations are reasons to keep conclusions tied to the outcomes and analyses actually posted.

11. Confidence Intervals and Precision

Precision concerns how tightly the data constrain the estimated difference. For the recalculated primary risk difference, the confidence interval includes zero. This means the posted summary statistics are compatible with no difference as well as with effects in either direction over the interval. The interval’s width cautions against treating the point estimate alone as a definitive description of the underlying difference.

The registry’s sponsor analysis reports a 95% confidence interval from -9.7 to 3.2 for its risk difference estimate of -3.3. This interval also includes zero. A 95% confidence interval is generated by a method that, under its assumptions and repeated use, would cover the target quantity in 95% of repetitions. It does not mean there is a 95% probability that this one interval contains the true value. The sponsor analysis method is not reported in the registry record, so the interval should be interpreted as the sponsor-reported result rather than as a fully reproducible calculation.

Confidence intervals are more informative than a point estimate alone because they display uncertainty and a range of compatible effects. They do not determine whether an effect is clinically important: that requires a relevant clinical threshold, which is not reported in the registry record. In a non-inferiority setting, the interval must be considered relative to the prespecified margin. Because that margin is not reported in the registry record, the sponsor interval cannot be used to independently assess the non-inferiority criterion.

The recalculation and sponsor analysis are based on posted results but are not described as methodologically identical. Their values should therefore be considered in context rather than combined. Both convey uncertainty, and neither interval alone establishes equivalence. A confidence interval that includes zero does not prove that the groups are the same; it indicates that the data do not exclude zero difference under that analysis.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning scenarios derived from the observed effect, not the trial’s original design calculation. For these binary outcomes, the figures are participants per arm, not a total across arms and not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a target effect set to the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance. Power is a design property calculated for a particular assumed effect, test, significance level, and allocation; it is not a guarantee that a study will produce a statistically significant result.

The rows that plan for 100% of the observed effect use the full recalculated effect as the assumed target. The rows for 75% and 50% use progressively smaller assumed effects. Smaller effects need more participants to distinguish them from no difference with the same target power, so the planning figures rise as the assumed effect is reduced. This relationship is a general feature of statistical planning, not evidence that a future study would observe any particular effect.

The registry record does not report the trial’s original sample-size assumptions or justification. The displayed planning figures are not observed power; observed power is not a useful substitute for interpreting the actual estimate and its confidence interval. These illustrations are conditional calculations, and they do not show what the trial was originally designed to detect or whether its original target was achieved.

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 = 0.588; treatment proportion p₁ = 0.616; average p̄ = 0.602.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6923 = 1.3568.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6920 = 0.5824.
4. n = (1.3568 + 0.5824)² / (0.0278)² = 4,873.5, rounded up to 4,874 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 <- 0.587973273942094                          # control proportion
p1 <- 0.615751789976134                          # 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(3788967)
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 = 4,874 (80% power), 6,524 (90% power)
 75% of observed effect: n per arm = 8,691 (80% power), 11,634 (90% power)
 50% of observed effect: n per arm = 19,609 (80% power), 26,251 (90% power)
power.prop.test: 4873.5 
Simulated power at n = 4,874 per arm: 0.804 (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 identifies a sponsor-reported non-inferiority analysis for the primary outcome. It gives a risk difference of -3.3 and a 95% confidence interval from -9.7 to 3.2. The analysis method and non-inferiority margin are not reported in the registry record. Without the margin, its direction convention, and the full analysis specification, the non-inferiority criterion cannot be checked independently from the posted interval.

The recalculation uses the posted group counts and is an unadjusted risk-difference comparison, with direction defined as ertapenem minus TBPM-PI-HBr. Its unadjusted p-value is 0.404, and its confidence interval includes zero. This calculation is a simple check from summary statistics, not a replacement for the sponsor’s analysis or a reconstruction of the trial’s full statistical plan. The two results may differ in analysis method or conventions; those details are not reported.

The registry discrepancy indicator is false, but this does not establish that the methods are identical or supply the missing non-inferiority margin. The sponsor result should be described as the trial’s reported analysis, while the recalculation should be described as an unadjusted summary-statistic comparison. Neither should be expanded into a stronger claim than the information supports.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, assessment times, populations, or contrasts. Even if each analysis uses a conventional significance threshold, the chance of at least one apparently unusual result can rise across a collection of analyses. Common approaches include prespecifying a hierarchy, adjusting significance thresholds, or treating secondary analyses as descriptive. The strategy used for this trial is not reported in the registry record.

The record lists 32 outcome measures and 25 analyses, with numerous secondary outcomes covering overall response, clinical cure, and sustained clinical cure across different populations and times. Those analyses should not be treated as though each independently confirms the primary result. The registry record does not say which secondary outcomes were prespecified for formal inference, whether any multiplicity adjustment was made, or how the primary and secondary tests were ordered.

Missing data and analysis-population choices are also important. The primary endpoint requires both a clinical assessment and microbiological information, and the listed analysis populations differ. The complete rules for inclusion in Micro-ITT, Microbiologically Evaluable, and clinically evaluable populations are not reported in the registry record. The handling of participants who lack endpoint data, have an unevaluable culture, or discontinue is also not reported in the registry record. No imputation or other missing-data method can be assumed.

The trial’s original sample-size justification, planned analysis details, interim analyses, and the non-inferiority margin are not reported in the registry record. These omissions prevent a complete evaluation of the planned inferential framework. They do not invalidate the posted counts, but they limit conclusions about whether analyses followed a prespecified plan and how multiplicity, missingness, and non-inferiority were handled.

Accordingly, the primary analysis is the central result for interpretation, while secondary findings are best treated as supporting descriptions. Readers should keep the population, endpoint definition, time point, and analysis type attached to each estimate. A finding in one evaluable population or at one visit cannot automatically be generalized to a different population or assessment time.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyelonephritis acute (0.3%), myocardial ischaemia (0.1%), pyrexia (0.1%), intervertebral discitis (0.1%), perirectal abscess (0.1%).

The registry reports serious adverse events among 685 participants at risk in the TBPM-PI-HBr group, with 14 affected, and among 687 at risk in the ertapenem group, with 12 affected. It also reports other adverse events among 685 at risk in the TBPM-PI-HBr group, with 39 affected, and among 687 at risk in the ertapenem group, with 30 affected. Deaths are listed as zero in each group.

These are counts in the registry’s safety reporting, not a complete account of event severity, duration, relatedness, or clinical consequences. The record lists acute pyelonephritis at 0.3% among the top serious-event terms, and myocardial ischaemia, pyrexia, intervertebral discitis, perirectal abscess, and retroperitoneal abscess at 0.1% each. The listed terms do not establish that events were caused by treatment. The registry record does not report enough detail to compare event timing, attribution, or exposure-adjusted rates.

Safety counts should be interpreted alongside the definitions of the safety population and event reporting. Those definitions and the complete adverse-event profile are not reported in the registry record excerpt. Differences in counts are descriptive and should not be treated as evidence of a safety advantage or disadvantage without fuller context and appropriate analysis.

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

The primary result addresses a specific question: combined clinical cure and microbiological eradication at test of cure in the Micro-ITT population. The posted counts show participants meeting that endpoint in both treatment groups. The unadjusted recalculation has an interval that includes no difference, so the summary statistics do not clearly establish a difference between groups in either direction.

This does not mean that the treatments are equivalent. Failure to establish a difference is not proof that the outcomes are identical; equivalence requires a prespecified margin and an analysis designed to evaluate it. Nor can the sponsor’s non-inferiority label be independently verified from the reported interval alone, because the margin and complete method are not reported in the registry record. The sponsor result should be kept distinct from the recalculation.

The endpoint is a combined measure at a single defined assessment time. It does not by itself describe every aspect of clinical course, all microbiological findings, longer-term outcomes, or the full safety profile. Secondary analyses address other populations and times, but those analyses do not automatically broaden the primary result. The record’s incomplete definitions and missing-data rules further limit generalization across populations.

The study is randomized and masked according to the registry, which are relevant design features for a treatment comparison. However, details of allocation procedures, masking roles, adherence, protocol deviations, and the complete statistical plan are not reported in the registry record. Those details can affect how confidently results are interpreted and applied beyond the analyzed data.

Accordingly, the statistical result is best read as an uncertain comparison of the posted primary endpoint counts, accompanied by a sponsor-reported non-inferiority analysis whose criterion cannot be independently checked from the registry information. It is not medical advice and does not establish that either treatment should be selected for an individual patient.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis population and endpoint definition matter as much as the treatment labels. The primary outcome requires both clinical improvement and microbiological eradication, and it is evaluated in a specified Micro-ITT population at Day 19. Counts from this analysis answer a more precise question than a broad statement about all enrolled participants or about symptoms alone.

It also shows why absolute effects and uncertainty should be read together. A point estimate gives a direction and magnitude on a chosen scale, while the confidence interval shows how much uncertainty remains. In this study, the recalculated interval includes no difference; that is a reason to avoid treating the point estimate as conclusive. It is not proof of exact equality.

The sponsor’s non-inferiority analysis highlights a further statistical distinction. Non-inferiority is not the same as a conventional test for any difference, and it relies on a prespecified margin. A registry report without the margin or complete method cannot support an independent assessment of the criterion. Keeping the sponsor analysis separate from an unadjusted recalculation is essential to avoid giving either result more meaning than it has.

Finally, multiple populations, outcomes, and assessment times make selective emphasis a risk. The secondary outcomes provide context, but without a reported multiplicity plan they should not be treated as a collection of confirmatory tests. Taken together, these features make the trial a useful example of how registry results can inform statistical interpretation while still leaving important design and analysis questions unresolved.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the non-inferiority margin or the method used for the sponsor’s reported non-inferiority analysis. Consequently, the sponsor interval cannot be assessed against its decision criterion from the registry information alone. The record also does not provide the original sample-size justification, so the rationale for the enrollment target is not available.

The primary Micro-ITT definition is incomplete in the record, and complete definitions for the other analysis populations are not reported. Rules for missing clinical or microbiological endpoint data, exclusions after randomization, imputation, and sensitivity analyses are not reported in the registry record. These issues are important for a combined endpoint that requires multiple kinds of data.

The available recalculation is unadjusted and uses posted summary counts. It does not reproduce a full protocol-defined analysis, account for covariates, or establish that its direction and estimand match the sponsor analysis. The sponsor method is not identified in the posted analysis summary. The record also does not report the multiplicity strategy for the many listed outcomes and analyses, or whether interim analyses were planned or conducted.

Although randomization and masking are identified, procedural details about allocation concealment, masking roles, adherence, treatment discontinuation, and protocol deviations are not reported in the registry record. The arm description for TBPM-PI-HBr is truncated, leaving part of its dosing qualifications unavailable. The safety summary gives counts and selected serious-event terms, but does not provide enough information about attribution, timing, exposure, or the full event profile.

These limitations do not change the posted counts. They do constrain how far the estimates can be generalized, how precisely the sponsor’s non-inferiority conclusion can be evaluated, and whether secondary results should be treated as confirmatory.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy, Safety and Pharmacokinetics of Orally Administered Tebipenem Pivoxil Hydrobromide (SPR994) Compared to Intravenous Ertapenem in Participants With Complicated Urinary Tract Infection (cUTI) or Acute Pyelonephritis (AP) — NCT03788967.
• Registry record last updated 2022-07-25; status last verified 2022-06.
• Results first posted 2022-07-25.
• 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 Phase 3 parallel-group study of oral TBPM-PI-HBr and intravenous ertapenem in participants with complicated urinary tract infection or acute pyelonephritis. Enrollment is listed as 1372. The trial used a double-dummy approach, with placebo tablets or infusion accompanying the active treatment administered by the other route.

The primary outcome was overall response, combining clinical cure and microbiological eradication at test of cure on Day 19 in the Micro-ITT population. The registry lists 264 of 449 participants responding in the TBPM-PI-HBr group and 258 of 419 in the ertapenem group. An unadjusted recalculation has a confidence interval that includes no difference; the registry also reports a sponsor non-inferiority analysis, but its margin and method are not reported in the registry record.

Secondary outcomes span other populations and assessment times. The record includes safety counts and selected serious adverse-event terms. Missing-data procedures, the multiplicity plan, and several details needed to reproduce the sponsor analysis are not reported in the registry record.