Safety and Tolerability of Ertapenem Sodium in the Treatment of Complicated Urinary Tract Infections (0826-055): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Tolerability of Ertapenem Sodium in the Treatment of Complicated Urinary Tract Infections (0826-055) (NCT01014013), a randomized phase 3 study. The primary outcome is Microbiological Response Assessment Profile.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group study sponsored by Merck Sharp & Dohme LLC. The official title describes a prospective, multicenter, partially-blinded, randomized comparative study of INVANZ and ceftriaxone sodium in adults with complicated urinary tract infections. The registry's design fields identify the study as randomized, parallel, and double-masked. The record therefore uses different wording for masking in the title and the design fields; further detail reconciling those descriptions is not reported in the registry record.

The registry lists 271 participants enrolled. The primary efficacy analysis, however, included 137 evaluable patients, with 66 in the MK0826 group and 71 in the ceftriaxone group. Safety outcome denominators were reported separately. These populations serve different purposes: the efficacy result applies to the stated evaluable population, while the safety counts use their own at-risk denominators. The record does not report a full participant-flow account or the reasons for the difference between enrolled and analyzed populations.

The study start is recorded as 2008-04 and primary completion as 2009-02. Its status is completed. The registry record describes the overall purpose as evaluating safety, tolerability, and efficacy, with the primary efficacy question centered on favorable microbiological response after therapy. The posted outcome timeframe is 5 to 9 days post-therapy. Detailed treatment schedules, the masking procedures, the planned allocation ratio, and the original statistical design assumptions are not reported in the registry record. Randomization and the parallel-group structure describe the broad comparison, but they do not by themselves establish how missing outcomes or departures from assigned treatment were handled.

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: 1 patient was excluded due to ineligibility. The patient had a positive at screening pregnancy test.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Primary efficacy analysis was done for 137 evaluable patients (66 patients from MK0826 and 71 patients from Ceftriaxone)

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 Microbiological Response Assessment Profile, measured over 5 to 9 days post-therapy.

The primary endpoint is the microbiological response assessment profile, recorded as the number of participants and focused on favorable response at 5 to 9 days post-therapy. The registry describes the principal contrast as the difference in favorable microbiological response rates between MK0826 and ceftriaxone. In practical terms, each participant is classified according to whether the response meets the study's favorable-response definition, and the group response rates are compared. The exact microbiological criteria underlying that classification are not reported in the registry record.

A microbiological endpoint is used to assess response at the level of the infection-related organisms, rather than relying only on clinical symptoms. It can therefore address a different aspect of response from a clinical assessment. Neither type of endpoint, on its own, captures every possible consequence of treatment or the longer-term course after the stated assessment period. The registry also lists a clinical response assessment at the same timeframe as a secondary outcome.

The analyzed counts are 58 favorable responses among 66 evaluable patients in the MK0826 group and 63 among 71 in the ceftriaxone group. Those counts describe the recorded analysis population, not necessarily every participant enrolled or randomized. Interpretation depends on both the response definition and the selection of evaluable patients; the registry record does not give further detail about either the response-classification rules or the evaluability criteria.

7. Results Posted in the Registry

• Ceftriaxone: 88.7% (63/71) versus 87.9% (58/66) on control; risk difference 0.9 percentage points (95% CI -9.9 to 11.6), risk ratio 1.01 (0.89–1.14); unadjusted two-proportion z-test p = 0.876.

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.

Clinical Response Assessment Profile

• 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:
  • Ceftriaxone: 98.6% (70/71) versus 97.0% (64/66) on control; risk difference 1.6 percentage points (95% CI -3.3 to 6.6), risk ratio 1.02 (0.97–1.07); unadjusted two-proportion z-test p = 0.517.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ceftriaxone and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists one secondary outcome: a clinical response assessment at 5 to 9 days post-therapy. The broad pattern across the primary microbiological assessment and the secondary clinical assessment is similar in that the recalculated comparisons point in the same direction, while neither provides a precise separation between the groups. The clinical outcome addresses a different dimension of response from the microbiological endpoint, so alignment in direction does not make the outcomes interchangeable or turn the secondary result into confirmation of the primary result.

Secondary results generally carry less inferential weight than a prespecified primary outcome, especially when the analysis plan does not state how multiple outcomes were handled. Examining several outcomes can increase the chance of an apparently notable result arising by chance. An unadjusted result does not account for that possibility. The registry record does not report a multiplicity adjustment or a hierarchy for testing the secondary outcome, so the secondary finding should be treated as supportive descriptive information rather than independent proof.

The record does not report whether the secondary outcome was prespecified in the original protocol, whether its assessment criteria were fixed in advance, or whether the analysis population and missing-data rules matched those for the primary endpoint. Those details affect how strongly the secondary result can corroborate the primary analysis. The broad agreement in direction is a descriptive feature of the posted comparisons, not a basis for a formal combined conclusion.

The secondary result also cannot resolve the limits of the primary analysis population or the missing methodological details. It supplies a related clinical perspective at the same assessment timeframe, but it does not establish longer-term outcomes, equivalence, or non-inferiority. Any interpretation should retain the distinction between the primary microbiological endpoint and the secondary clinical assessment.

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

• Clinical Response Assessment Profile

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary: each evaluable participant contributes to a favorable-response count or does not. The response rate is the number with a favorable response divided by the number analyzed in that group. A comparison of two such rates can be expressed on several scales. The risk difference subtracts one rate from the other; the risk ratio divides one rate by the other; and the odds ratio compares the odds of response between groups. Each measure answers a related but distinct question, so its scale and direction need to be stated.

What does the risk difference tell the reader?

The recalculated primary risk difference is 0.009, defined as the ceftriaxone rate minus the MK0826 rate. A value of zero corresponds to equal rates on this scale. A positive value indicates a higher observed rate in the first group named in that subtraction, while a negative value indicates a higher observed rate in the second group. The sign is meaningful only alongside the group order. The sponsor-reported contrast uses the reverse order, MK0826 minus ceftriaxone, so its signed estimate should not be compared without first noting that difference in direction.

The risk difference is often useful because it describes an absolute separation between response rates. The risk ratio and odds ratio instead describe relative contrasts. Relative measures can look different from an absolute measure because they use different scales. None of these measures, by itself, establishes whether a finding is clinically important; that requires an appropriate context and a prespecified interpretation, neither of which is posted by a statistical estimate alone.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the observed data under the method used to construct it. It communicates uncertainty around an estimate, rather than identifying the exact true effect or assigning a probability to each value in the interval. The primary recalculated 95% confidence interval, -0.099 to 0.116, spans zero. For a risk difference, zero is the value associated with equal response rates. The interval thus does not rule out equality, and it also allows differences in either direction. Its width is important: a near-zero point estimate does not ensure a precise estimate.

For a ratio measure, the value representing no relative difference is one. The posted risk-ratio and odds-ratio intervals include one. These intervals therefore also leave substantial uncertainty about the direction and size of a relative contrast. A confidence interval should be interpreted with the outcome definition, analysis population, and comparison direction in view.

What does the p-value contribute?

The unadjusted p-value for the primary recalculated comparison is 0.876. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. A large p-value does not prove there is no difference; it means the data do not provide strong evidence against the null under the stated test. The registry does not report the method used to calculate this p-value, so its exact testing procedure is not reported in the registry record.

The word “unadjusted” matters because it indicates that the reported value has not been adjusted for multiplicity. If multiple outcomes or comparisons are examined, repeated testing can increase the chance of at least one apparently unusual result. The record does not report a multiplicity strategy. The primary outcome is distinguished in the record, but the statistical plan for managing other analyses is not reported in the registry record.

What is the distinction between the registry analysis and the recalculation?

The sponsor-reported primary analysis gives a difference between two response rates of -0.8, with a 95% confidence interval from -11.7 to 10.2, and is labeled as a non-inferiority or equivalence analysis. The recalculated risk difference is reported on a proportion scale and uses the reverse group order. These estimates should not be treated as numerically identical: the displayed scales and direction differ. The registry does not name the sponsor's statistical method, and it does not report a p-value for that analysis. The sponsor analysis and the unadjusted recalculation therefore have distinct roles and should be read with their definitions intact.

In general, an analysis labeled non-inferiority asks whether the data rule out an unacceptable loss relative to a prespecified margin. An equivalence analysis asks whether the plausible difference lies within prespecified bounds in both directions. The confidence interval alone cannot establish either claim without those bounds and the associated analysis plan. The margin and plan are not reported in the registry record.

Why do analysis populations matter?

The primary efficacy result uses 137 evaluable patients, while the registry records 271 enrolled. An evaluable analysis uses participants meeting the analysis criteria, but the criteria and exclusions are not reported in the registry record. Results can depend on who is included, particularly when participants lack an outcome assessment or do not follow assigned treatment. The record does not state how missing responses were handled, whether all randomized participants were analyzed as assigned, or whether a separate per-protocol population was used. These are not minor technical details: they affect the interpretation of the estimate and its uncertainty.

General statistical principles explain why these distinctions matter, but they cannot fill gaps in the trial record. The analysis method, missing-data handling, response criteria, and planned inferential framework are not reported in the registry record. Interpretation should therefore remain tied to the populations and calculations explicitly identified.

11. Confidence Intervals and Precision

The primary recalculated estimate is 0.009 for the risk difference, with a 95% confidence interval from -0.099 to 0.116. Because the interval includes zero, the data do not establish a nonzero difference on this scale. The interval also extends in both directions, so it remains compatible with a lower response rate in either group. The estimate should be read together with the interval: the point estimate is only one plausible summary of the comparison, while the interval displays substantial uncertainty around it.

The breadth of an interval matters as much as whether it crosses a reference value. A narrow interval can constrain plausible effects more tightly; a broad interval leaves more room for materially different possibilities. Here, the range is broad enough that a small point estimate should not be mistaken for a precise demonstration of similarity. The registry does not report a clinically acceptable difference threshold, so the interval cannot be classified as excluding differences that would matter clinically.

The risk-ratio interval, 0.894 to 1.141, and the odds-ratio interval, 0.383 to 3.082, also include their respective no-difference values. The odds-ratio interval is especially wide, reflecting considerable imprecision on that scale. Ratios and risk differences are not directly interchangeable, and the size of an interval depends partly on the effect measure used.

The sponsor-reported interval is -11.7 to 10.2 for its stated difference between response rates. It is expressed on a different scale and uses the reverse comparison direction from the recalculated risk difference. The registry record does not report the margin needed to interpret it as a non-inferiority or equivalence interval. Accordingly, it cannot independently support such a conclusion from the interval alone.

Precision is also limited by the analysis population: the primary analysis includes 137 evaluable patients, not all enrolled participants. Missing-outcome counts and reasons for exclusion are not reported in the registry record. The confidence intervals quantify uncertainty under the calculations used, but they do not account for unknown biases that could arise from outcome selection or missingness.

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 based on the observed effect, not the trial's original design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

For a binary outcome, the displayed figures are participants per arm, not total participants across both arms and not total events. The 80% power column describes the planned number per arm for a design that would have an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and model were correct. The 90% power column describes the corresponding planning target for a 90% chance. Higher target power generally requires a larger planned sample under otherwise unchanged assumptions.

For the primary outcome, the illustration lists 22,247 participants per arm for 80% power and 29,782 for 90% power when planning for 100% of the observed effect. Planning for 75% of the observed effect lists 39,864 participants per arm for 80% power and 53,366 for 90% power. Planning for 50% of the observed effect lists 90,396 participants per arm for 80% power and 121,014 for 90% power. The pattern reflects the general principle that smaller effects are harder to distinguish from random variation and therefore require more participants.

The curve represents the same kind of planning relationship across effect assumptions; it is not a record of what the trial achieved. These calculations are illustrations, not observed power. They should not be used to infer that the completed study had a particular probability of finding a result after its outcomes were known. They also do not replace a prospective design calculation based on a clinically justified target effect and the planned analysis.

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 = 0.879; treatment proportion p₁ = 0.887; average p̄ = 0.883.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4545 = 0.8907.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4544 = 0.3825.
4. n = (0.8907 + 0.3825)² / (0.0085)² = 22,246.7, rounded up to 22,247 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 <- 0.878787878787879                          # control proportion
p1 <- 0.887323943661972                          # 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(1014013)
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 = 22,247 (80% power), 29,782 (90% power)
 75% of observed effect: n per arm = 39,864 (80% power), 53,366 (90% power)
 50% of observed effect: n per arm = 90,396 (80% power), 121,014 (90% power)
power.prop.test: 22246.7 
Simulated power at n = 22,247 per arm: 0.801 (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 sponsor-reported primary analysis records a difference between two response rates of -0.8, with a 95% confidence interval from -11.7 to 10.2. It is labeled as a non-inferiority or equivalence analysis. The registry record does not identify the statistical method or report a p-value for this analysis. It also does not report the margin required to interpret the result as a formal non-inferiority or equivalence finding.

The recalculated risk difference is 0.009, with a 95% confidence interval from -0.099 to 0.116, and is expressed as ceftriaxone minus MK0826. The sponsor's description instead defines the contrast as MK0826 minus ceftriaxone, and its posted values are on a different displayed scale. The opposite subtraction order explains why the signs should not be compared as if they represented the same direction. The estimates also differ in presentation, so the recalculation should not be substituted for the sponsor's stated analysis.

The registry record does not flag a discrepancy between the posted data and the recalculation. The recalculation is an unadjusted calculation from the posted summary statistics; it does not reproduce an undocumented sponsor model. The sponsor analysis should be understood according to its stated contrast and label, while recognizing that essential details for evaluating its non-inferiority or equivalence framework are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary microbiological outcome and one posted secondary clinical outcome. It does not report a multiplicity plan, such as a testing hierarchy, adjustment method, or rule for interpreting multiple outcome analyses. The unadjusted p-value for the recalculated primary comparison therefore should not be understood as adjusted for examining additional outcomes. General statistical reasoning treats repeated testing as relevant because the chance of at least one apparently unusual result can increase when many hypotheses are examined.

Missing-data handling is not reported in the registry record. The primary efficacy population is described as 137 evaluable patients, but the record does not define evaluability, list reasons for exclusion, state how absent response assessments were treated, or identify an imputation or sensitivity-analysis approach. The number enrolled is 271, and the efficacy result should not be assumed to represent all enrolled participants. Without a participant-flow account, it is not possible to determine whether exclusions could have affected the observed comparison.

The record does not identify an intention-to-treat analysis, a per-protocol analysis, or the analysis population specified in the original protocol beyond the stated evaluable population. It also does not report how treatment deviations were handled. These omissions matter for randomized trials because inclusion rules can affect both the estimated treatment contrast and the assumptions supporting a formal non-inferiority assessment.

Interim analyses and stopping rules are not reported in the registry record. The original sample-size justification, planned significance level for the primary outcome, analysis method, non-inferiority margin, and response-classification criteria are also not reported. These absences do not show that such procedures were not used; they mean the registry record does not establish what they were. As a result, the posted estimates can be described, but the full prespecified inferential framework cannot be reconstructed.

16. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebrovascular accident (0.8%), hydrocephalus (0.8%), somnolence (0.8%), sleep apnoea syndrome (0.8%), pyelonephritis acute (0.8%).

The serious adverse event figures are reported for 132 participants at risk in the MK0826 group and 135 in the ceftriaxone group. Serious adverse events affected 12 participants in the MK0826 group and 8 in the ceftriaxone group. Other adverse events affected 85 and 90 participants, respectively, using those same group-specific at-risk denominators. These are participant counts as recorded, not estimates of a treatment effect adjusted for differences between groups.

The registry lists Cerebrovascular accident, Hydrocephalus, Somnolence, Sleep apnoea syndrome, Pyelonephritis acute, and Sepsis among the top serious terms, each recorded as 0.8%. The record does not state a group attribution for each listed term in the information available, so they should not be assigned to a particular treatment group. It also does not report deaths in these safety summaries.

Safety counts require context: the denominators differ from the efficacy analysis population, and the registry record does not provide detail about event collection, severity grading, causal attribution, or follow-up. Counts alone do not establish that an event was caused by a study treatment, and differences in counts should not be interpreted as a definitive comparative safety conclusion.

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

The posted results describe response assessments in the evaluable patients included in the primary analysis. The observed counts and recalculated risk difference do not establish a clear separation between the groups, and the confidence interval remains compatible with differences in either direction. This is an uncertainty statement about the available data, not evidence that the treatments are identical.

The sponsor's reported analysis is labeled non-inferiority or equivalence, but the registry record does not report the margin or analysis method needed to assess that label fully. A formal non-inferiority conclusion depends on a prespecified acceptable difference and a confidence interval evaluated against that margin. A formal equivalence conclusion similarly requires prespecified bounds. The fact that an interval includes zero is not, by itself, evidence of equivalence or non-inferiority.

The primary endpoint concerns favorable microbiological response at 5 to 9 days post-therapy. It does not, by itself, establish the course of symptoms beyond the assessment timeframe, longer-term outcomes, or every dimension of safety. The record includes a clinical response assessment as a secondary outcome, but that result does not replace the primary endpoint or resolve the limitations in its analysis population and precision.

The analysis also does not justify a treatment recommendation. The results are specific to the trial's recorded population, endpoint definitions, timeframe, and analysis. Detailed eligibility criteria, missing-data methods, response definitions, and original statistical assumptions are not reported in the registry record. Those gaps constrain how broadly the findings can be generalized and how confidently formal claims can be made.

The most defensible reading is therefore descriptive and bounded: the posted efficacy summaries show similar observed response counts in the analyzed groups, while the uncertainty intervals do not rule out differences in either direction. That reading neither proves equal effects nor demonstrates a meaningful advantage or disadvantage.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be read in isolation. The recalculated primary risk difference is close to zero, yet its confidence interval is broad and includes both zero and values on either side. The practical statistical message is not simply that the estimate is small; it is that the estimate is imprecise enough to leave a wide range of effects compatible with the data.

It also highlights the importance of stating comparison direction. The sponsor analysis defines the contrast as MK0826 minus ceftriaxone, while the recalculated risk difference is ceftriaxone minus MK0826. Reversing the order changes the sign without changing the underlying comparison. A reader who ignores that convention could mistakenly interpret the estimates as disagreeing.

The record also distinguishes an observed analysis population from the number enrolled. The primary efficacy result uses evaluable patients, whereas the safety summaries use separate at-risk denominators. Clear reporting of populations and participant flow is essential because different denominators answer different questions. Without the missing details, the relationship between the randomized population and the efficacy estimate remains uncertain.

Finally, the registry's non-inferiority or equivalence label demonstrates why labels alone are not enough. Interpretation requires a prespecified margin, method, and analysis population. Their absence in the registry record limits the ability to assess the formal claim. The case is a useful reminder that effect estimates, uncertainty, endpoint definitions, and design assumptions all contribute to statistical interpretation.

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 primary limitation specific to interpreting this trial is that the efficacy analysis is reported for 137 evaluable patients, while 271 participants were enrolled. The registry record does not define the evaluability criteria, explain exclusions, provide participant flow, or state how missing assessments were handled. The resulting estimate therefore cannot be assumed to represent every enrolled or randomized participant.

The endpoint is described as favorable microbiological response, but the exact classification criteria are not reported in the registry record. The sponsor analysis is labeled non-inferiority or equivalence, yet the margin, statistical method, and formal decision criteria are not reported. This prevents independent assessment of that claim from the posted summary alone. The response assessment timeframe is specified, but longer-term outcome information is not reported in the record.

The official title calls the study partially blinded, while the registry design fields identify double masking. The registry record does not explain that difference or describe the masking procedures. The trial is also described as multicenter in the official title, but details about sites are not reported in the registry record.

The registry does not report the original sample-size justification, the detailed statistical plan, multiplicity handling, interim analyses, or stopping rules. It also does not provide dosing details in the record. These gaps limit reconstruction of the planned analysis and assessment of the context for the observed precision. They do not establish that such procedures or details were absent from the original study; they are simply not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Tolerability of Ertapenem Sodium in the Treatment of Complicated Urinary Tract Infections (0826-055) — NCT01014013.
• Registry record last updated 2017-03-22; status last verified 2017-02.
• Results first posted 2010-03-01.
• 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 record describes a completed phase 3 randomized comparative study of ertapenem sodium (MK0826/Invanz) and ceftriaxone sodium in adults with complicated urinary tract infections. It lists 271 enrolled participants and identifies the primary outcome as favorable microbiological response at 5 to 9 days post-therapy. The primary efficacy analysis included 137 evaluable patients.

The recalculated primary risk difference is 0.009, with a 95% confidence interval from -0.099 to 0.116 and an unadjusted p-value of 0.876. The interval includes zero and allows differences in either direction; it does not establish equivalence. The sponsor's posted analysis is labeled non-inferiority or equivalence, but the margin and method are not reported in the registry record.

The record also includes a secondary clinical response assessment and safety counts. Missing-data methods, detailed response criteria, multiplicity handling, and original design assumptions are not reported in the registry record, limiting interpretation of the planned inferential framework.