A Safety and Tolerability Study of Doripenem Compared With Cefepime in Children Hospitalized With Complicated Urinary Tract Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety and Tolerability Study of Doripenem Compared With Cefepime in Children Hospitalized With Complicated Urinary Tract Infections (NCT01110408), a randomized phase 3 study. The primary outcome is The Number of Participants With Clinical Cure Rate at Test Of Cure (TOC) Visit.

2. Clinical Question

The registry describes a safety and tolerability study, and clinical cure is the posted primary outcome. That outcome gives a clinical-response measure at a specified follow-up visit; it does not by itself capture all aspects of safety, tolerability, or microbiological response. The central statistical comparison is between the posted cure counts in the doripenem and cefepime groups. The registry record does not report a formal analysis plan or an adjusted treatment-effect analysis.

3. Trial Design

This was a Phase 3, randomized, parallel-group, quadruple-masked study described as prospective, double-blind, and multicenter in its official title. It compared doripenem with cefepime in hospitalized children with complicated urinary tract infections. The registry lists enrollment as 41 and trial status as terminated. The recorded start was 2010-12, and primary completion was 2013-06.

The arm descriptions specify intravenous dosing every 8 hours. Doripenem was given at 20 mg/kg per dose, up to 500 mg per dose, as a 60-minute infusion. Cefepime was given at 50 mg/kg per dose, up to 2 g per dose, as a 30-minute infusion. Each description allowed at least 3 days of intravenous therapy, either alone or followed by oral amoxicillin/clavulanate potassium or ciprofloxacin, and a total treatment duration of 10 to 14 days. These are the planned treatment descriptions in the registry, not evidence that every participant received the full regimen.

For the primary endpoint, the displayed arm counts are 20 participants with clinical cure among 30 in the doripenem group and 5 among 10 in the cefepime group. The endpoint results therefore come from smaller displayed groups than the overall enrollment figure. The registry record does not explain the difference between the enrollment figure and the endpoint group sizes, nor does it provide participant-flow details explaining exclusions, missing endpoint assessments, or treatment discontinuations.

The registry includes placebo interventions alongside the active drugs, consistent with the stated masking, but it does not describe the precise masking procedures or identify which roles were masked. It also does not report the reason for termination. The original study design assumptions, including any sample-size justification or planned recruitment target by arm, are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Clinical Intent-to-Treat (CITT): All randomized participants who met the minimal disease definition of complicated urinary tract infection regardless if a baseline pathogen was isolated from the pretreatment urine culture.

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 The Number of Participants With Clinical Cure Rate at Test Of Cure (TOC) Visit, measured over TOC (7 to 14 days after the last dose of study medication therapy).

The primary endpoint is the number of participants classified as having clinical cure at the test-of-cure visit. The assessment was scheduled 7 to 14 days after the last dose of study medication. For the registry’s cure classification, participants had to have resolution or clinical improvement in signs and symptoms of complicated urinary tract infection, no fever, no additional antimicrobial therapy required for the infection, and an improvement assessment at the end-of-IV visit.

This endpoint is used to represent a clinical response at a defined point after treatment, rather than relying only on a change during intravenous therapy. The criteria combine symptoms and signs with the need for further antimicrobial treatment, while also requiring an earlier improvement assessment. Because the registry defines the measure as a participant count, the posted result is a binary outcome at the participant level: each participant either met the stated cure definition or did not.

The specified analysis population is the Clinical Intent-to-Treat group. It includes randomized participants who met the minimal disease definition of complicated urinary tract infection, regardless of whether a baseline pathogen was isolated from the pretreatment urine culture. The posted primary results give the cure counts by arm, but the registry record does not explain how missing or unevaluable test-of-cure assessments were handled. Nor does it report a separate analysis population or a formal adjusted estimate for this endpoint.

7. Results Posted in the Registry

• Cefepime: 50.0% (5/10) versus 66.7% (20/30) on control; risk difference -16.7 percentage points (95% CI -52.0 to 18.6), risk ratio 0.75 (0.38–1.46); unadjusted two-proportion z-test p = 0.346.

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.

The Number of Participants With Clinical Improvement Rate at End of IV (EIV) Visit

• 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:
  • Cefepime: 100.0% (10/10) versus 93.3% (28/30) on control; risk difference 6.7 percentage points (95% CI -2.3 to 15.6), risk ratio 1.07 (0.97–1.18); unadjusted two-proportion z-test p = 0.402.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cefepime and the control. The interval gives the range of effects that remain compatible with the data.

The Number of Participants With Clinical Cure Rate at Late Follow-Up (LFU) Visit

• 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:
  • Cefepime: 50.0% (5/10) versus 60.0% (18/30) on control; risk difference -10.0 percentage points (95% CI -45.6 to 25.6), risk ratio 0.83 (0.42–1.65); unadjusted two-proportion z-test p = 0.580.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cefepime and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover clinical response at the end of intravenous therapy, clinical cure at late follow-up, and microbiological responses at several visits. Taken together, they extend the primary test-of-cure clinical outcome across time and include measures that address pathogen response as well as clinical status. The registry posts six secondary outcomes, but only two secondary outcomes have group counts and comparison summaries in the recorded results included for this analysis. The other listed outcomes do not have posted results in the registry record.

The available secondary results do not create a precise or uniform pattern that resolves the primary uncertainty. Like the primary comparison, they are based on small displayed groups, and their intervals include the null values. Their results can provide context about the observed clinical course and later outcomes, but they cannot substitute for a better-powered primary comparison or establish a consistent treatment effect across all endpoints.

In general, secondary outcomes are often interpreted as supportive or exploratory, particularly when many outcomes are assessed. Testing multiple outcomes creates more opportunities for apparently notable results to occur by chance. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a plan distinguishing confirmatory from exploratory secondary analyses. The secondary comparisons are unadjusted, and their p-values should therefore carry less weight than a prespecified primary analysis would carry.

The record also does not report how missing secondary assessments were handled or whether all listed measures were analyzed in the same population. These gaps make it difficult to compare outcomes across visits or judge whether differences in analysis populations affect the apparent pattern. The safest reading is that the secondary measures add descriptive context, but the available results do not overcome the uncertainty and reporting limitations of the primary endpoint.

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

• The Number of Participants With Clinical Improvement Rate at End of IV (EIV) Visit
• The Number of Participants With Clinical Cure Rate at Late Follow-Up (LFU) Visit
• The Number of Participants With Favorable Per-participant Microbiological Response
• Number of Participants With Favorable Per-pathogen Microbiological Outcome Rate at End of IV (EIV) Visit
• Number of Participants With Favorable Per-pathogen Microbiological Outcome Rate at Test Of Cure (TOC) Visit
• Number of Participants With Sustained Favorable Per-pathogen Microbiological Outcome Rate at Late Follow-Up (LFU) Visit

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as having clinical cure or not having clinical cure at the test-of-cure visit. For a binary outcome, the basic descriptive result is the number meeting the endpoint relative to the number in the analysis group. The registry posts 20 of 30 for doripenem and 5 of 10 for cefepime. The reported comparisons use doripenem as the reference group and express the contrast for cefepime relative to it.

What does a risk difference describe?

A risk difference compares the observed outcome proportions by subtracting one group’s proportion from the other. It is expressed on the absolute proportion scale, which makes it useful for describing how far apart the group outcomes are in direct terms. The posted risk difference is -0.167, with a confidence interval that extends from a negative value to a positive value. Because that interval includes zero, the data do not rule out no difference on this scale. The sign depends on the comparison direction: the reported value is for cefepime relative to doripenem.

What does the risk ratio describe?

A risk ratio compares the outcome proportion in one group with the proportion in the reference group. A value of 1 represents equal proportions. The posted risk-ratio estimate is 0.75, and its interval runs from 0.384 to 1.465. Since that interval includes 1, it is also compatible with no difference on the relative scale. Risk differences and risk ratios answer related but distinct questions: one describes an absolute separation, while the other describes a relative comparison. Neither measure removes the uncertainty caused by limited outcome counts.

How should the p-value be read?

The unadjusted p-value is 0.346. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. Here it is a recalculated, unadjusted result from the posted summary statistics. No sponsor-reported primary analysis is listed in the registry record, and the reported analyses count is 0.

Why does a confidence interval matter?

In general, a confidence interval describes uncertainty around an estimate under the method used to construct it. A broad interval indicates that a range of effects remains compatible with the data and assumptions. When an interval includes the null value, the observed data do not clearly distinguish the estimate from no difference at the corresponding confidence level. This does not establish equivalence or prove that the groups have identical outcomes. An equivalence or noninferiority conclusion would require an appropriate prespecified margin and analysis, neither of which is reported in the registry record.

Why are the calculations unadjusted?

The posted endpoint data give group counts and denominators, and the displayed comparison is a simple unadjusted comparison of those summaries. An adjusted analysis could account for prespecified covariates or design features, but no such model or covariate plan is reported. Without those details, the unadjusted comparison is the appropriate description of the available summary results, not a claim that it was the trial’s planned or only analysis.

What can small groups mean for inference?

In general, limited numbers of participants and outcome events produce less stable estimates and wider uncertainty intervals. A small change in the observed outcome counts can substantially change a group proportion or comparison. That matters because the endpoint results are based on 30 participants in the doripenem group and 10 in the cefepime group. Randomization supports a planned comparison, but it does not make estimates precise when the posted groups are small. The registry record does not provide enough detail to assess the role of missing outcome data or any factors affecting the randomized groups after allocation.

The secondary outcomes are also binary participant or pathogen response measures. Their reported counts and unadjusted comparisons can be read using the same general principles, while recognizing that multiple endpoint testing adds another source of uncertainty. The record does not describe a multiplicity strategy, a hierarchy of secondary hypotheses, or a statistical analysis plan. Consequently, secondary p-values, where posted, should not be treated as confirmatory evidence without those details.

11. Confidence Intervals and Precision

The primary estimate is imprecise. Its risk-difference confidence interval crosses zero, and the risk-ratio interval, 0.384 to 1.465, crosses 1. Both intervals therefore include values consistent with no difference, while also allowing effects in either direction. The point estimate alone cannot identify the size or direction of the underlying effect with confidence.

In general, confidence intervals communicate the range of values compatible with the observed data under the statistical method and its assumptions. They are not guarantees that the true effect lies within the interval, and their width reflects uncertainty rather than clinical importance. An interval spanning the null does not demonstrate equivalence; it indicates that the data do not precisely distinguish the observed contrast from no difference. No equivalence margin is reported in the registry record.

The small displayed endpoint groups are important to precision. With 30 participants in the doripenem group and 10 in the cefepime group, the observed proportions are sensitive to individual outcomes, especially in the smaller group. The registry record does not report an adjusted interval, a prespecified precision target, or a formal sample-size rationale. The posted uncertainty should therefore be read as a limitation of the available results, not as evidence that a clinically meaningful difference is absent.

Interpretation is further constrained because the record does not explain missing or unevaluable primary assessments, provide participant flow, or report an inferential analysis plan. These details would help assess whether the posted denominator and analysis population were handled as intended and whether additional uncertainty should be considered.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. The posted planning table is for the primary outcome and gives 137 and 182 participants per arm for 100% of the observed effect; 240 and 320 for 75% of the observed effect; and 529 and 708 for 50% of the observed effect. The sample-size assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation, with the effect set to the stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the original trial design assumptions, which are not reported in the registry record.

The 80% power column describes the planned group size for a hypothetical study designed to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column uses a higher target chance of detecting that effect, and consequently gives larger planning figures. The rows illustrate the effect-size assumption: when the effect to detect is a smaller fraction of the observed effect, more participants per arm are needed under the same assumptions. This is not observed power.

These figures do not establish what enrollment the trial originally intended, and they should not be read as evidence that the trial had any particular power. They are sensitive to the observed effect used as their starting point, which itself is uncertain in the small posted groups. The registry record does not report the trial’s own sample-size justification, recruitment assumptions, or planned analysis parameters beyond the separate planning illustration.

The trial is a binary-outcome study, so the figures are participants per arm rather than total events. In general, a power calculation is conditional on assumptions about the effect, allocation, significance level, and statistical method; changing those assumptions changes the planning result. The posted illustration should therefore be used to understand how assumed effect size relates to hypothetical group size, not as a retrospective verdict on trial quality.

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 = 0.667; treatment proportion p₁ = 0.500; average p̄ = 0.583.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6972 = 1.3665.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6872 = 0.5783.
4. n = (1.3665 + 0.5783)² / (-0.1667)² = 136.2, rounded up to 137 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 <- 0.666666666666667                          # control proportion
p1 <- 0.5                          # 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(1110408)
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 = 137 (80% power), 182 (90% power)
 75% of observed effect: n per arm = 240 (80% power), 320 (90% power)
 50% of observed effect: n per arm = 529 (80% power), 708 (90% power)
power.prop.test: 136.2 
Simulated power at n = 137 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

The registry lists one primary outcome and six secondary outcomes. Multiple outcome assessments can increase the chance of finding at least one apparently unusual result even when no underlying effects are present. Statistical plans commonly address this issue through prespecified testing sequences or adjustment methods. The registry record does not report whether either approach was planned or used, so no multiplicity-adjusted interpretation can be made from the posted information.

The primary outcome comparison is presented as an unadjusted recalculation from the posted summary counts, with a p-value of 0.346. The registry records 0 analyses, and there are no reported analyses for the posted secondary outcomes. There is no discrepancy flag for the recalculated primary comparison. Since no sponsor-reported inferential analysis is listed, the recalculation should be understood as a descriptive statistical comparison rather than a reconstruction of an undocumented analysis plan.

The primary population is defined as the Clinical Intent-to-Treat group: randomized participants meeting the minimal disease definition, regardless of whether a baseline pathogen was isolated. The record does not report a separate per-protocol or safety population for these outcomes. It also does not specify how missing test-of-cure assessments, withdrawals, or unevaluable outcomes were treated. The endpoint group counts are posted, but participant flow and reasons for differences between enrollment and endpoint group sizes are not reported in the registry record.

Missing-data handling can affect binary endpoint comparisons if outcome availability differs between groups or is related to response. General statistical methods may use different assumptions for missing outcomes, and those assumptions can change estimates. Without information on missingness, imputation, or sensitivity analyses, it is not possible to assess how robust the posted results are to those issues.

The original statistical analysis plan, any interim analyses, and the reason for termination are also not reported in the registry record. No conclusions should be drawn about whether these procedures occurred. Their absence from the record limits assessment of how the posted outcome selection, analysis population, and multiplicity were determined.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: urinary tract infection (20.0%), pseudomembranous colitis (10.0%), pyelonephritis acute (10.0%), pyuria (3.3%).

The adverse-event summaries report serious adverse events among 1 of 30 participants in the doripenem group and 3 of 10 in the cefepime group. Other adverse events are reported for 11 of 30 participants in the doripenem group and 6 of 10 in the cefepime group. These are participant counts in the recorded groups; they are descriptive and do not establish that a treatment caused an event or that one treatment is safer.

The registry lists Urinary Tract Infection at 20.0%, Pseudomembranous Colitis at 10.0%, Pyelonephritis Acute at 10.0%, and Pyuria at 3.3% among the top serious terms. The record does not provide enough context in these summaries to determine the full event-level detail or relationship to study treatment. Death counts are not reported in the registry record.

Group sizes are small, and the summaries should be interpreted with that limitation in mind. A numerical difference in adverse-event counts is not, by itself, a reliable estimate of comparative risk. The registry record does not provide a formal comparative safety analysis, adjustment for exposure duration, or details sufficient to assess causality.

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

The posted primary result is a comparison of clinical cure counts at the test-of-cure visit, using the registry-defined Clinical Intent-to-Treat population. The observed group proportions differ, with 20 of 30 participants meeting the cure definition in the doripenem group and 5 of 10 in the cefepime group. The unadjusted comparison is imprecise: its risk-difference interval includes zero, its risk-ratio interval includes 1, and the unadjusted p-value is 0.346.

These results do not establish that the treatments are equivalent, nor do they establish a reliable difference between them. A nonsignificant comparison is not proof of no effect. Demonstrating equivalence or noninferiority would require a prespecified margin and an appropriate design and analysis, which are not reported in the registry record. The broad uncertainty leaves a range of possible effects compatible with the posted data.

The clinical-cure endpoint is only one part of the trial’s stated safety-and-tolerability purpose. The secondary clinical and microbiological measures add other perspectives, but the available secondary results are also limited and the registry does not report multiplicity procedures. Safety counts are descriptive and do not establish causation or comparative safety. No medical conclusion should be drawn from these summaries alone.

The registry record reports a terminated study and enrollment of 41, but does not report the reason for termination or the original sample-size rationale. The endpoint groups are smaller than the enrollment figure, and participant flow and missing-outcome handling are not reported. These omissions make it difficult to understand how the posted result relates to the full conduct of the study. The most defensible interpretation is therefore narrow: the registry posts an observed difference in cure counts, accompanied by substantial uncertainty and limited analysis detail.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate is not enough to interpret a randomized comparison. The observed cure counts differ between the groups, but the uncertainty intervals include the null values. A reader must consider both the direction of the estimate and the range of effects compatible with the data. The posted p-value alone cannot describe the size or importance of the difference.

It also highlights the effect of small endpoint groups on precision. When group counts are limited, each participant can materially affect the observed proportion, and confidence intervals can remain broad. This is especially important when interpreting secondary outcomes, which add multiple comparisons without a reported adjustment strategy.

The registry record also demonstrates the difference between an outcome count and an analysis plan. Posted counts allow simple unadjusted comparisons, but they do not reveal how missing assessments were handled, which covariates might have been prespecified, or whether any interim analyses took place. Those details are needed to fully evaluate the evidential role of the calculations.

Finally, hypothetical sample-size planning figures should not be confused with the study’s original design or its achieved ability to answer the clinical question. The registry does not report the original sample-size justification, while the posted planning illustration depends on the observed effect. Separating those details helps readers avoid treating a retrospective planning scenario as an account of the trial’s intended design.

18. Limitations

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

Several limitations specific to this record constrain interpretation. First, the trial is marked terminated, but the reason is not reported in the registry record. The record also gives enrollment as 41 while the displayed primary endpoint groups are 30 and 10; it does not provide participant flow or explain the difference. This prevents assessment of how enrollment, randomization, follow-up, and endpoint availability relate to one another.

Second, the primary comparison is based on small displayed groups and has broad uncertainty. The registry lists no reported analyses, and the posted comparison is an unadjusted recalculation from summary counts. There is no reported adjusted analysis, analysis plan, or sponsor-reported inferential result against which to compare it.

Third, missing-outcome handling is not reported. The record does not explain whether participants without an evaluable test-of-cure assessment were excluded, classified in a particular way, or addressed through sensitivity analyses. This matters because the posted outcome counts alone cannot show how unavailable assessments were treated.

Fourth, the registry lists several secondary outcomes but does not report a multiplicity plan or a hierarchy of tests. Only some secondary outcomes have results posted in the record. That limits the ability to assess the full planned outcome set and to distinguish confirmatory findings from exploratory ones.

Finally, details of masking procedures, the reason for termination, and the trial’s original sample-size justification are not reported. The safety summaries are descriptive, and the registry does not provide a formal comparative safety analysis or enough detail to establish event causality. These limitations do not change the posted counts, but they restrict the conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Safety and Tolerability Study of Doripenem Compared With Cefepime in Children Hospitalized With Complicated Urinary Tract Infections — NCT01110408.
• Registry record last updated 2014-07-15; status last verified 2014-07.
• Results first posted 2014-07-02.
• 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

NCT01110408 is a Phase 3 randomized, parallel-group study comparing doripenem with cefepime in hospitalized children with complicated urinary tract infections or pyelonephritis. It is described as quadruple-masked and multicenter, and its registry status is terminated. The recorded start was 2010-12, primary completion was 2013-06, and enrollment was 41.

The primary outcome was clinical cure at the test-of-cure visit, assessed 7 to 14 days after the last dose. The posted cure counts were 20 of 30 for doripenem and 5 of 10 for cefepime. The unadjusted comparison is imprecise, with intervals including no difference and an unadjusted p-value of 0.346. The record does not report the reason for termination, the original sample-size justification, missing-outcome handling, or a formal statistical analysis plan.