Methenamine Hippurate Versus Trimethoprim in the Prevention of Recurrent UTIs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Methenamine Hippurate Versus Trimethoprim in the Prevention of Recurrent UTIs (NCT03077711), a randomized phase 4 study. The primary outcome is Time to Subsequent Infection as Defined From Time of Treatment Initiation to Recurrence of UTI.

2. Clinical Question

The study’s stated primary objective was to determine whether there is a difference in prevention of recurrent UTIs between methenamine hippurate and daily suppressive antibiotics. The posted primary measure makes that question concrete by recording time from treatment initiation to a subsequent infection. A longer mean time would describe later recurrence on average within the participants represented in the posted outcome data. It does not, by itself, describe the proportion who had a recurrence, the number of recurrences per participant, or the timing of every individual event.

The trial also set out to assess medication tolerability and adverse effects over a given 1 year time period. The named secondary outcomes include adverse effects, medication adherence, and bacterial infection prevalence and types. The primary comparison and the secondary outcomes address different aspects of the study question: the primary measure concerns time until recurrence, while the secondary measures concern treatment experience and infection characteristics. The registry record does not report a more detailed primary hypothesis or the original statistical analysis plan.

3. Trial Design

This was a randomized, phase 4, parallel-group trial with no masking. The registry record lists Endeavor Health as the sponsor, a start date of 2016-06, primary completion on 2019-06-21, and study status as completed. Enrollment was 92. The two treatment arms were methenamine hippurate and trimethoprim, assigned to participants diagnosed with recurrent UTIs.

Random allocation is intended to create groups whose baseline characteristics are comparable on average, reducing the risk that treatment assignment is systematically related to participant characteristics. Randomization does not guarantee that the groups will be identical, particularly in a trial of this size, and the registry record does not give baseline characteristics for assessing their balance. The allocation method beyond the description “randomized” is not reported in the registry record.

The trial was unmasked: participants and study personnel were not described as blinded to treatment assignment. Lack of masking can affect experiences and behavior, reporting of symptoms or adverse effects, and decisions about whether an event represents recurrence. The registry description says participants were advised to follow up for recurrence symptoms or at 6 and 12 month intervals if symptom-free. It does not give further details about how recurrence was confirmed or adjudicated.

The primary outcome summaries report 43 participants in each arm. Those outcome counts do not account for all 92 enrolled participants, and the reasons or analysis-population rules are not reported in the registry record. The posted secondary adherence summaries involve different, smaller group counts. Whether those counts reflect missing measurements, eligibility rules, or another selection process is not reported. The trial’s detailed protocol, original sample-size assumptions, and analysis populations are also 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:

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 Time to Subsequent Infection as Defined From Time of Treatment Initiation to Recurrence of UTI, measured over up to 12 months.

The primary endpoint is time in days from treatment initiation to recurrence of a UTI, summarized as a mean with a standard deviation. Its stated timeframe is up to 12 months. The registry description says participants were advised to follow up if they experienced symptoms of recurrence and, if symptom-free, at 6 and 12 month intervals.

Time to recurrence is used because it captures when a subsequent infection occurs, rather than only whether an infection occurred during follow-up. A comparison of mean times can therefore describe whether recurrence tended to happen earlier or later in the observed groups. The posted outcome, however, is a continuous summary of time, not a report of individual event times or a full time-to-event analysis. The registry record does not report how participants without a recurrence were handled in calculating the means, whether censoring was used, or how the endpoint was defined and confirmed beyond the title’s description.

The mean is sensitive to the distribution of observed times: a small number of relatively long or short times can influence it. The standard deviation describes the spread of individual observations around the group mean; it is not the uncertainty in the estimated mean difference. The reported comparison supplies a separate interval for the between-arm difference, which is more directly relevant to the precision of that contrast. Interpretation should remain tied to the posted definition and follow-up period rather than treating the mean as a complete account of recurrence patterns.

7. Results Posted in the Registry

• Patients With Recurrent UTIs Arm 2: mean 119.00 versus 101.00 on control; difference 18.00 (95% CI -19.76 to 55.76), standardized effect d = 0.20; z-test p = 0.350.

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.

Morisky Medication Adherence Survey

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Patients With Recurrent UTIs Arm 2: mean 6.94 versus 7.28 on control; difference -0.34 (95% CI -1.13 to 0.45), standardized effect d = -0.26; z-test p = 0.399.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patients With Recurrent UTIs Arm 2 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address medication adherence, adverse effects, and bacterial infection prevalence and types. They complement the primary time-to-recurrence outcome by describing treatment-taking behavior, tolerability, and infection characteristics. They do not replace the primary endpoint: a secondary measure can provide context, but it does not directly resolve uncertainty in the primary comparison.

The posted adherence summary compares mean Morisky Medication Adherence Survey scores, with different participant counts from those used in the primary outcome summary. Its unadjusted comparison is imprecise and does not establish a clear between-arm difference. The registry record lists adverse effects and bacterial infection prevalence and types as secondary outcomes, but does not report a full set of numerical results and analyses for each named outcome. Serious and other adverse-event counts are recorded separately in the safety information.

Across the reported secondary information, there is no basis for a strong claim that the arms differ consistently across outcomes. The adherence data are limited to the participants represented in that measure, while the other listed outcomes do not have complete posted analyses. Differences in available counts and the absence of detailed outcome definitions make it difficult to compare the secondary evidence directly with the primary result.

Unadjusted secondary results carry less weight for several reasons. Multiple outcomes create multiple opportunities for apparently notable results to arise through chance, particularly if many comparisons are examined. The registry record does not report whether a multiplicity strategy was prespecified or whether any adjustment was made. Secondary results can also be less complete or less precise than the primary result, and the analysis populations may differ. These concerns do not make secondary outcomes irrelevant; they mean they should be treated as supportive and exploratory unless a prespecified analysis plan establishes otherwise. That plan is not reported in the registry record.

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

• Adverse Effects
• Morisky Medication Adherence Survey
• Bacterial Infection Prevalence and Types

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure: elapsed time in days, summarized by a mean and standard deviation for each arm. The posted group summaries are 101.0 days with a standard deviation of 84.4 in the methenamine hippurate arm and 119.0 days with a standard deviation of 94.0 in the trimethoprim arm. A mean gives a single measure of the group’s average observed time. A standard deviation describes how dispersed the participant observations are around that average; it does not directly describe how precisely the group mean has been estimated.

What does the mean difference represent?

The reported mean difference is 18.0 days, with trimethoprim as arm 2 and methenamine hippurate as arm 1. The sign and direction depend on this ordering: a positive estimate means the arm 2 mean is greater than the arm 1 mean. The estimate is a difference between group averages, not a statement that each participant’s time differed by that amount. It also does not describe the distribution of individual outcomes or establish that the groups differ beyond sampling variation.

How should the interval be read?

The reported interval for the mean difference runs from -19.76 to 55.76 days. A confidence interval is a range of values compatible with the observed data under the statistical method and its assumptions. In repeated use of a valid method, intervals constructed this way have a specified coverage property; the registry record does not state the confidence level for this interval. Because the interval includes zero, the posted comparison does not distinguish the observed estimate from no mean difference under the interval’s method. Its width also signals that the data do not pin down the contrast precisely. An interval is not a range within which every individual participant’s outcome lies.

What does the p-value add?

The posted unadjusted p-value is 0.35. A p-value measures how compatible the observed result, or a more extreme result, is with a null model and the assumptions of the test. It does not give the probability that the null hypothesis is true, nor does it quantify the size or importance of a difference. The word “unadjusted” indicates that the reported comparison is not described as adjusted for other variables or for multiple comparisons. The registry record does not identify a sponsor-reported primary analysis or explain whether this p-value matches the original planned method.

Why can variation matter?

The standard deviations are large relative to the difference between the group means, and the posted interval reflects uncertainty in the estimated contrast. In general, greater variation makes a mean difference harder to estimate precisely when other aspects of a study are unchanged. Means and standard deviations may also be less informative when data are strongly skewed or influenced by unusual observations. The registry record does not report the outcome distribution, diagnostic checks, or a transformation or alternative analysis. It is therefore not possible to determine from the posted summaries alone whether the assumptions underlying a mean-based comparison were examined.

General statistical explanation: over-dispersion refers to variation greater than a model expects. If it is present, uncertainty estimates from a model that understates the variation can be too small, and inferential conclusions can be misleading. The posted outcome is summarized with standard deviations, but the registry record does not report a model-based assessment of over-dispersion or any corresponding adjustment. This concept is relevant as a general issue in analyzing variable clinical outcomes, not as a claim that over-dispersion occurred in this trial.

What is different about a time-to-event analysis?

Although the outcome concerns time to recurrence, the posted primary result is a comparison of means. A time-to-event approach can use information about when events occur and account for participants whose event time is not observed during follow-up through censoring methods. Such methods require details about event definitions, follow-up, and censoring. The registry record does not report a time-to-event model, a hazard ratio, a Kaplan–Meier estimate, or the handling of participants without a recorded recurrence. None should be inferred from the mean comparison. The endpoint’s name alone does not show that a survival-analysis method was used.

The trial is randomized, which supports a causal comparison when assignment is preserved in the analysis and follow-up and outcome measurement are adequately handled. But the record does not state whether the primary results follow an intention-to-treat approach, whether participants were analyzed as randomized, or how deviations from assigned treatment were handled. Randomization does not resolve bias introduced by missing outcomes or selective inclusion after assignment. These uncertainties limit how fully the posted estimates can be interpreted.

The comparison statistics are simple, unadjusted recalculations from posted summary statistics. The discrepancy indicator is false, so there is no flagged conflict between the recalculation and a sponsor analysis. No sponsor-reported analyses are listed. This distinction matters: a recalculation can check and describe the arithmetic relationship among posted summaries, but it cannot reconstruct an unreported prespecified analysis, covariate adjustment, or missing-data procedure. The registry record does not report the statistical analysis plan, interim analyses, or the trial’s original sample-size justification.

11. Confidence Intervals and Precision

The primary mean difference is 18.0 days, and its reported interval ranges from -19.76 to 55.76 days. The interval includes zero and spans values compatible with either a lower or higher mean in the trimethoprim arm relative to methenamine hippurate. It therefore conveys substantial uncertainty about the direction and size of the difference. The exact coverage level for this interval is not reported in the registry record, so it should not be assigned a confidence level that is not stated.

The point estimate is only one possible value consistent with the data and method. The interval makes clear that the evidence does not locate the true mean difference precisely. Its inclusion of zero is consistent with the unadjusted p-value of 0.35, but the interval gives more information about a range of plausible contrasts than a p-value alone. Neither statistic establishes equivalence: an equivalence conclusion would require a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

Precision is affected by the number of observations and by outcome variability. The primary summaries include 43 participants per arm, with standard deviations of 84.4 and 94.0 days. The registry record does not explain why the primary outcome counts differ from total enrollment, whether any outcomes were missing, or how such observations were handled. Those omissions make it difficult to assess whether the interval captures all relevant sources of uncertainty. The posted interval should therefore be read as uncertainty for the reported comparison, not as a guarantee that other sources of uncertainty have been addressed.

The outcome is reported as means, while the registry record does not describe the distribution of individual times or the handling of participants without a recurrence. A mean-based interval may not describe the data well if its assumptions are unsuitable. No distributional checks or alternative primary analysis are reported. The precision indicated by the interval is meaningful for the reported summary comparison, but it does not answer every question about recurrence patterns or follow-up.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For this continuous primary outcome, the figures are participants per arm, 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 planning scenario uses a stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under those planning assumptions, if that effect is the true one and the assumed model is suitable. The 90% power column uses the same kind of interpretation with a higher target chance of detection. Power is a property of a planned design under assumptions; it is not the probability that a particular result is correct.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how the required sample size changes when the target difference changes. A smaller target effect is harder to distinguish from random variation, so it requires more participants for the same target power under otherwise unchanged assumptions. These figures are sensitive to the observed effect used as their starting point. They are not a reconstruction of what investigators planned before the trial, and they are not observed power.

The planning illustration does not account for design features or analysis choices that are not included in its stated assumptions. In particular, the registry record does not report the trial’s original target effect, its original sample-size calculation, or details of any planned adjustment. The estimates should be read as hypothetical planning guidance tied to the stated assumptions, not as a verdict on whether the completed trial was adequate for its original objectives.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 18.000; pooled standard deviation σ = 89.329.
2. n = 2 × (1.96 + 0.842)² × 89.329² / 18.000² = 386.6, rounded up to 387 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
delta <- 18                      # observed difference in means
sigma <- 89.3290546239016                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3077711)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 387 (80% power), 518 (90% power)
 75% of observed effect: n per arm = 688 (80% power), 921 (90% power)
 50% of observed effect: n per arm = 1,547 (80% power), 2,071 (90% power)
power.t.test: 387.6 
Simulated power at n = 387 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 record lists a primary outcome and several secondary outcomes, but it does not report a statistical analysis plan describing how the outcome family was prioritized or how multiplicity was handled. Multiplicity arises when several outcomes or comparisons are assessed: even if each analysis is individually valid, examining many results can increase the chance of at least one apparently unusual finding. General approaches include prespecifying a hierarchy, adjusting inferential thresholds, or treating secondary analyses as exploratory. The record does not say which, if any, approach was planned.

No sponsor-reported analyses are listed. The primary and adherence comparisons available in the posted results are unadjusted recalculations from summary statistics. The primary comparison has an unadjusted p-value, but the registry record does not report whether it was the prespecified primary test, whether it was adjusted for covariates, or whether other analyses were conducted. Interim analyses are not reported in the registry record. It would be inappropriate to assume either that interim analyses occurred or that they did not occur.

Missing-data handling is also not reported. The primary summaries include 43 participants in each arm, whereas enrollment is 92. The record does not explain the difference, state how many participants had an observed primary endpoint, or describe imputation, censoring, or other methods for incomplete follow-up. The adherence summaries include different arm counts, and the reason for those counts is not reported. These differences may reflect several possible processes, but the registry record does not permit a determination of which applied.

The analysis populations are not named. It is therefore not reported whether participants were analyzed according to randomized assignment, treatment received, or another rule. The record also does not give information about treatment discontinuation, protocol deviations, or exclusions from the analyses. These details matter because excluding participants after randomization can affect the balance created by random assignment. Without the analysis population and missing-data approach, the posted estimates can be described but cannot be fully evaluated for susceptibility to selection bias.

The registry record does not report the original sample-size justification, the detailed protocol, or a prespecified strategy for interpreting primary and secondary results. These omissions limit the ability to distinguish planned confirmatory analyses from analyses that may be exploratory. They also prevent assessment of whether the posted outcome summaries represent all participants and analyses intended by the study design.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety information reports serious adverse events among 47 participants at risk in the methenamine hippurate arm and 45 at risk in the trimethoprim arm. The number recorded as affected by serious adverse events is 0 in each arm, and deaths are 0 in each arm. These figures describe the recorded safety information; they do not establish that serious events could not occur or that the treatments have identical safety profiles.

Other adverse events are reported for 6 of 47 participants at risk in the methenamine hippurate arm and 4 of 45 at risk in the trimethoprim arm. The registry record does not provide the individual event terms in the posted serious-event list, which is empty, and does not give further detail about the nature, severity, timing, or relationship of other adverse events to treatment. The figures should be read as counts of affected participants, not as a complete description of all event episodes.

Safety comparisons are difficult to interpret without details about ascertainment, follow-up duration for each participant, and event definitions. The record does not report those methods. The numbers are descriptive and should not be used alone to conclude that one treatment is safer than the other.

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

The primary result describes the mean time to subsequent UTI in the participants represented by the posted arm summaries. The trimethoprim arm has a higher reported mean than the methenamine hippurate arm, and the estimated difference is 18.0 days. The interval from -19.76 to 55.76 days includes zero and allows a range of possible differences in either direction. The unadjusted p-value of 0.35 likewise does not provide clear evidence of a difference under the reported comparison.

This does not show that the treatments are equivalent. Failure to establish a difference can reflect imprecision as well as a genuinely small difference, and the interval remains compatible with effects in both directions. Equivalence or non-inferiority requires a prespecified margin and an appropriate design and analysis; those are not reported in the registry record. Nor does a higher mean in one arm establish that the treatment is beneficial for an individual participant.

The outcome focuses on time to recurrence, not every clinically relevant feature of recurrent infection. The posted mean does not identify the proportion of participants who experienced recurrence, the number of infections per participant, or the distribution of times. The record does not report how participants without a recurrence were handled in the calculation. Follow-up was described as up to 12 months, so the result should not be generalized to longer periods on the basis of these data.

Randomization supports a comparative interpretation, but the record lacks detail about outcome ascertainment, analysis populations, and missing data. The primary outcome count is 43 per arm, and the reasons for the difference from total enrollment are not reported. These limitations mean the result cannot be fully assessed for potential effects of incomplete follow-up or analysis choices. The trial’s open-label design is also relevant because knowledge of assignment may affect symptom reporting or assessment, though the registry record does not establish that such effects occurred.

The result is therefore best understood as an imprecise comparison of posted mean times in this completed trial. It does not prove a difference, prove no difference, establish equivalence, or settle questions about the broader prevention of recurrent UTIs. Any interpretation beyond the recorded participants, outcome definition, and follow-up would require additional information not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an estimated effect and the certainty around it. The mean difference is positive, but the interval spans zero and values in both directions. Reading the point estimate alone would overstate what the data establish; the interval and the unadjusted p-value show that the comparison is imprecise.

It also demonstrates why a randomized design is only part of the evidence. Random allocation can reduce confounding at baseline, but interpretation still depends on outcome measurement, follow-up, the analysis population, and missing-data handling. The registry describes an open-label study and follow-up advice, yet does not report key details of endpoint confirmation or analysis methods. Those gaps limit how confidently the posted summaries can be connected to the original clinical question.

The primary measure is expressed as a mean time, while the clinical concept is recurrence during follow-up. These are related but not interchangeable. The mean difference gives a concise contrast, but it does not describe event proportions, repeated infections, or the distribution of recurrence times. Knowing what a summary captures—and what it leaves out—is central to statistical interpretation.

The planning illustrations also show how sample-size estimates depend on the effect assumed for planning. Smaller target effects require more participants under otherwise unchanged assumptions. Because the figures are based on the observed effect rather than the trial’s original design calculation, they should not be used as evidence about what investigators planned or as a retrospective judgment of observed power.

Finally, the record includes multiple secondary outcomes, but does not report a multiplicity strategy or a full set of secondary analyses. That makes it important to distinguish the primary comparison from supporting descriptive information and to avoid selecting a single secondary finding as decisive. The trial offers useful comparative data, while its uncertainty and reporting gaps define the limits of what can be concluded statistically.

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 are specific to the information reported for this trial. The study was unmasked, so participants and personnel knew the assigned treatment. The registry record does not explain how recurrence was confirmed or whether outcome assessment used standardized criteria. These details matter for an outcome based on symptoms and subsequent infection.

The primary summaries include 43 participants per arm, while enrollment was 92. The record does not explain the difference or identify the analysis population. It also does not state how participants without an observed recurrence, incomplete follow-up, or treatment discontinuation were handled. The different counts in the adherence outcome add to the uncertainty about which participants contributed to each measure.

The primary outcome is presented as a mean and standard deviation. No distributional description, individual event-time information, or time-to-event analysis is reported. The registry record also does not state whether participants without recurrence were censored or otherwise included in the mean calculation. This limits assessment of whether the summary captures the follow-up experience appropriately.

Although the study was randomized, the allocation process and any concealment procedures are not reported. Baseline characteristics are also not included in the posted results, so balance between arms cannot be assessed from this record. The protocol, original sample-size justification, prespecified analysis plan, multiplicity approach, and interim analyses are not reported in the registry record.

Finally, only limited numerical secondary information is available. The named secondary outcomes are not accompanied by a complete set of reported analyses, and the safety information does not give detailed event descriptions or ascertainment methods. These reporting limitations do not establish that particular methods were absent from the study; they mean that such methods are not reported in the registry record and cannot be evaluated from it.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Methenamine Hippurate Versus Trimethoprim in the Prevention of Recurrent UTIs — NCT03077711.
• Registry record last updated 2020-01-14; status last verified 2020-01.
• Results first posted 2020-01-14.
• 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

NCT03077711 is a completed, randomized, unmasked, parallel-group phase 4 trial sponsored by Endeavor Health. It enrolled 92 participants with recurrent UTIs and compared methenamine hippurate with trimethoprim.

The primary outcome was mean time in days from treatment initiation to subsequent infection, with follow-up up to 12 months. The posted summaries report means of 101.0 days and 119.0 days, and an unadjusted mean difference of 18.0 days with an interval from -19.76 to 55.76 days and p = 0.35. The interval includes zero and indicates substantial uncertainty about the difference.

The registry record lists adherence, adverse effects, and bacterial infection prevalence and types as secondary outcomes. It does not report the original sample-size justification, detailed analysis plan, analysis populations, or missing-data methods. The posted estimates describe the available results but do not establish equivalence or a definitive difference between treatments.