Nutraceutical Efficacy for rUTI: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nutraceutical Efficacy for rUTI (NCT03395288), a randomized phase 2, phase 3 study. The primary outcome is Incidence of Symptomatic, Culture Proven Urinary Tract Infections.

2. Clinical Question

3. Trial Design

The registry identifies NCT03395288 as a randomized, controlled, parallel-group study, with phase listed as phase 2 and phase 3 and masking listed as single. It does not report whose masking was used or describe the masking procedures. The sponsor was Washington University School of Medicine. The record lists the study status as terminated.

The stated objective was to evaluate D-mannose as non-antibiotic prophylaxis for recurrent urinary tract infection in postmenopausal women using vaginal estrogen therapy. In the randomized comparison, participants were assigned to daily D-mannose powder or to a control condition with no additional intervention. The planned follow-up for the primary outcome was 90 days per participant. The registry also describes an observational group of women with recurrent urinary tract infections who had completed menopause but were not using vaginal estrogen and were followed while taking D-mannose. Because that group was observational, it should not be treated as a randomized comparator.

The registry reports 61 enrolled overall. Its primary outcome description specifies 57 randomized participants, with 28 assigned to treatment and 29 to control, and 4 in the observational arm. It also says that 44 participants started study day 1 across all three groups. The posted primary outcome results use 19 treatment participants and 25 control participants, while the observational-arm results use 2 participants. The record does not explain the relationship among these enrollment, study-day-one, and outcome denominators.

The treatment-arm instructions specify one level teaspoon of D-mannose powder in at least 200 ml of water once daily for 90 days. Controls were not to use an additional intervention. The observational-arm description mentions either D-mannose capsules or powder, but does not establish a randomized comparison for that group. The registry record does not report the trial’s original sample-size justification, detailed allocation procedures, or a complete statistical analysis plan.

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: Of the 61 patients consented, 4 patients were in the observational arm and 57 were in the RCT arm (28 treatment, 29 control).

Overall Study

Analysis population for the primary outcome, as defined in the registry: 57 patients were enrolled in the RCT(28 randomized to the treatment arm , 29 to the control arm). 4 participants in the Observational Arm. A total of 44 patients started study day1 across all three groups. Data was analyzed for 19 patients in the treatment arm and 25 patients in the control arm. Due to early termination and low recruitment in the Observational Arm, data on the 4 participants was not analyzed (1 withdrew prior to study day 1, 1 withdrew prior to completion - not study related).

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 Incidence of Symptomatic, Culture Proven Urinary Tract Infections, measured over each participant will be followed for 90 days during study enrollment.

The primary endpoint is the cumulative incidence of symptomatic, culture-proven urinary tract infection during 90 days of follow-up. The registry records the outcome as a count of participants with an event. A symptomatic episode supported by culture is a clinically specific outcome definition: it combines reported symptoms with microbiological confirmation rather than relying on symptoms alone. The endpoint therefore addresses the occurrence of qualifying infections during the stated follow-up period.

Cumulative incidence describes whether participants experienced the event during the follow-up window. It is useful for a prevention question because the comparison is between the proportions of participants with at least one qualifying event in each randomized arm, rather than the total number of infection episodes. The posted results report 6 participants with an event among 19 analyzed in the treatment arm and 12 among 25 analyzed in the control arm.

The registry also lists symptomatic culture-proven infections from D-mannose-susceptible uropathogens as a secondary outcome, along with side effects and symptomatic culture-proven infection among all participants taking D-mannose. These are related but distinct questions. The primary endpoint is the broad randomized comparison among women using vaginal estrogen; the observational group does not replace that randomized comparison. The registry record does not describe further rules for defining, adjudicating, or counting repeated infection events.

7. Results Posted in the Registry

• RCT Treatment Arm: 31.6% (6/19) versus 48.0% (12/25) on control; risk difference -16.4 percentage points (95% CI -45.1 to 12.2), risk ratio 0.66 (0.30–1.43); unadjusted two-proportion z-test p = 0.272.

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.

Incidence of Symptomatic Culture Proved UTI From D-mannose Susceptible Uropathogens

• 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:
  • RCT Treatment Arm: 31.6% (6/19) versus 40.0% (10/25) on control; risk difference -8.4 percentage points (95% CI -36.8 to 20.0), risk ratio 0.79 (0.35–1.79); unadjusted two-proportion z-test p = 0.565.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCT Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

Side Effects

• 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:
  • RCT Treatment Arm: 15.8% (3/19) versus 0.0% (0/25) on control; risk difference 15.8 percentage points (95% CI -0.6 to 32.2); unadjusted two-proportion z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCT Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Symptomatic, Culture Proven UTI in All Participants Taking D-mannose

• 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:
  • RCT Treatment Arm: 31.6% (6/19) versus 48.0% (12/25) on control; risk difference -16.4 percentage points (95% CI -45.1 to 12.2), risk ratio 0.66 (0.30–1.43); unadjusted two-proportion z-test p = 0.272.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RCT Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address related but distinct aspects of the study: infection attributed to D-mannose-susceptible uropathogens, side effects, and symptomatic culture-proven infection among participants taking D-mannose. Together, they broaden the descriptive picture beyond the primary randomized comparison. They should not be treated as interchangeable endpoints: a narrower microbiological definition and a safety outcome answer different questions from the primary cumulative-incidence comparison.

At a broad level, the posted secondary outcome comparisons do not remove the uncertainty in the primary result. The registry gives event counts and unadjusted comparisons, but does not report detailed sponsor analyses for the secondary outcomes. The results are therefore best interpreted as additional descriptive and exploratory evidence, rather than as independent confirmation of a single treatment effect. The observational participants also do not provide a randomized comparison with the control arm.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for chance findings. General statistical principle: if several hypotheses are tested, interpreting each result as though it were the only test can overstate the strength of evidence. A prespecified hierarchy or multiplicity adjustment can address this issue, but neither is reported in the registry record. The absence of a reported adjustment does not prove that none was used; it means the record does not document one.

The secondary outcomes are also subject to the study’s limited analyzed sample and the unexplained differences in participant counts. A pattern across outcomes can be useful context, but it cannot substitute for a clearly described analysis population, complete reporting of uncertainty, or a prespecified statistical approach. The secondary findings should be read in conjunction with the primary endpoint and its broad confidence interval.

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

• Incidence of Symptomatic Culture Proved UTI From D-mannose Susceptible Uropathogens
• Side Effects
• Incidence of Symptomatic, Culture Proven UTI in All Participants Taking D-mannose

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each person is counted according to whether a qualifying symptomatic, culture-proven urinary tract infection occurred during follow-up. The posted arm results give event counts and the number of participants represented in each randomized arm. This allows an arm-level risk comparison. The registry does not report a detailed model specification or a sponsor-authored statistical analysis for the primary endpoint.

What does the risk difference express?

The risk difference subtracts the control-arm event risk from the treatment-arm event risk. It is expressed on the risk scale, so a negative value indicates a lower observed risk in the treatment arm, while a positive value indicates a higher observed risk there. The posted estimate is -0.164. Its confidence interval, -0.451 to 0.122, includes zero, the value corresponding to no risk difference. The interval’s width signals substantial uncertainty about the size and direction of the contrast.

How do relative risk and odds ratio differ?

The relative risk compares the event risk in one arm with the event risk in the other. A value of 1 corresponds to equal risks; a value below 1 indicates a lower observed risk in the treatment arm. The posted relative risk is 0.658, with a confidence interval from 0.302 to 1.432. The odds ratio compares event odds rather than risks. Its posted estimate is 0.5, with a confidence interval from 0.144 to 1.737. The odds ratio and relative risk are different measures, and neither should be interpreted as a separate replication of the primary result. Both intervals include 1, their no-difference value.

What does the p-value tell the reader?

The posted unadjusted p-value for the primary comparison is 0.272. A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test; it is not the probability that the null hypothesis is true and does not measure the clinical importance of an effect. The registry record does not report the full test specification or an analysis plan that identifies a prespecified threshold for interpreting the p-value. The p-value should therefore be read alongside the event counts and confidence interval, not as a stand-alone verdict.

Why is the uncertainty substantial?

Confidence intervals around binary outcomes depend on the number of participants and events, among other assumptions. With relatively few analyzed participants and events, plausible underlying risks can remain compatible with the observed counts. General statistical principle: larger samples often narrow uncertainty intervals when the design and data quality are otherwise similar. This does not guarantee a particular result, nor does it remove possible bias from missing outcomes or departures from the analysis plan.

The posted comparison is unadjusted. The record does not describe adjustment for baseline characteristics, site, or other variables, and it does not report a detailed account of how participants were handled after randomization. It is therefore not possible to establish from the registry record whether the posted comparison follows an intention-to-treat approach, a per-protocol approach, or another analysis population definition. The treatment and control denominators in the outcome results are the ones relevant to interpreting those displayed estimates.

General statistical principle: adjustment can address specified sources of imbalance or improve precision, but it depends on the variables and model being prespecified and appropriately used. It cannot automatically correct missing outcomes or unmeasured differences. No adjusted estimates are reported in the registry record, so the posted unadjusted comparison should not be described as adjusted evidence.

Several related outcomes were recorded, including infection from D-mannose-susceptible uropathogens, side effects, and infection among all participants taking D-mannose. Testing multiple outcomes can increase the chance that at least one result appears unusual by chance. General statistical principle: multiplicity methods can control that risk, but the choice and use of such methods should be prespecified. The registry record does not report a multiplicity adjustment or a hierarchy for secondary outcomes. The unadjusted secondary p-values therefore warrant more caution than a single prespecified primary analysis would, and they do not replace the primary endpoint.

The registry lists the study as terminated, but does not report the reason for termination or whether stopping was related to efficacy, safety, recruitment, or another matter. It also does not report interim analyses or stopping rules. No conclusion about those procedures can be drawn from the termination status alone.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.164, and its confidence interval extends from -0.451 to 0.122. General statistical explanation: a confidence interval describes a range of values compatible with the observed data under the method’s assumptions. It is not a guarantee that the true effect lies within that particular interval, and it does not account for sources of bias that were not included in the analysis.

For the risk difference, zero represents no difference between arms. Because the interval includes zero, the posted data are compatible with no difference as well as with effects in either direction. The interval is broad relative to the point estimate, so the observed estimate is not precise enough to identify a narrow range of plausible differences. This uncertainty is consistent with the limited number of analyzed participants and events.

The relative-risk interval, 0.302 to 1.432, and odds-ratio interval, 0.144 to 1.737, also include their respective no-difference value of 1. They express the same underlying comparison on different scales. Their estimates should be considered together with the event counts, not as multiple independent confirmations.

Confidence intervals quantify sampling uncertainty under a statistical method. They do not show whether all randomized participants were included, resolve the unexplained enrollment and analysis denominators, or establish that outcome data were complete. The registry record does not report methods for handling missing data or a detailed sponsor analysis. Precision should therefore be interpreted in light of both the interval width and the incomplete reporting of the analysis population.

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 the randomized binary comparison, not total events. They are illustrations based on the observed effect, rather than the trial’s original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect. The trial’s own original sample-size justification is not reported in the registry record.

For planning for 100% of the observed effect, the illustration gives 139 participants per arm for 80% power and 185 participants per arm for 90% power. For planning for 75% of the observed effect, the corresponding figures are 251 and 336 participants per arm. For planning for 50% of the observed effect, they are 573 and 766 participants per arm. These are hypothetical planning requirements under the stated assumptions, not enrollment targets documented as the trial’s original plan.

In plain terms, the 80% power column describes the number of participants per arm that the calculation estimates would give an 80% chance of detecting the assumed effect under the model and significance level. The 90% column uses a higher desired chance of detecting that effect and therefore calls for more participants per arm. Smaller assumed effects require more participants to distinguish them from random variation. These figures are not observed power: they do not measure the probability that the completed trial found a true effect, and they do not change the interpretation of the observed result.

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 = 0.480; treatment proportion p₁ = 0.316; average p̄ = 0.398.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6922 = 1.3567.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6824 = 0.5743.
4. n = (1.3567 + 0.5743)² / (-0.1642)² = 138.3, rounded up to 139 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 <- 0.48                          # control proportion
p1 <- 0.315789473684211                          # 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(3395288)
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 = 139 (80% power), 185 (90% power)
 75% of observed effect: n per arm = 251 (80% power), 336 (90% power)
 50% of observed effect: n per arm = 573 (80% power), 766 (90% power)
power.prop.test: 138.3 
Simulated power at n = 139 per arm: 0.797 (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 record lists a primary outcome and several secondary outcomes, but does not report a hierarchy for testing them, a multiplicity adjustment, or a prespecified strategy for interpreting multiple comparisons. General statistical principle: testing several outcomes without accounting for multiplicity can increase the chance of apparently notable results arising by chance. This is one reason unadjusted secondary results should be treated cautiously. The registry record does not establish whether a multiplicity plan was present outside the registry.

The record reports 61 enrolled overall, including 57 randomized participants and 4 observational participants. It states that 44 participants started study day 1 across all three groups. The posted primary outcome counts use 19 treatment participants and 25 control participants; the observational outcome results use 2 participants. The registry does not explain how the 44 who started day 1 relate to these outcome denominators, or why the analyzed randomized-arm counts differ from the randomized enrollment counts.

That incomplete flow description matters because the interpretation of a randomized trial depends in part on knowing which participants contributed to each analysis and how post-randomization events were handled. The registry record does not report whether the primary analysis was intention-to-treat, per-protocol, or another approach. It does not describe missing-outcome methods, imputation, exclusions, or sensitivity analyses. These methods are not reported in the registry record.

The record also does not report interim analyses, stopping rules, or a statistical explanation for the terminated status. Termination alone does not establish why the study stopped or whether the decision was related to the results. Without those details, readers cannot assess whether early stopping, incomplete follow-up, or analysis choices affected the posted estimates.

These reporting gaps do not invalidate the observed counts, but they constrain what can be concluded from them. The displayed denominators should be read as the analysis populations represented in the posted outcomes, not as a complete account of every randomized participant.

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 registry reports zero serious adverse events among 27 participants at risk in the randomized treatment arm, zero among 29 at risk in the randomized control arm, and zero among 4 at risk in the observational arm. It also reports zero deaths in each group. No serious adverse-event terms are listed. These are the posted serious-event counts during the registry’s safety reporting period.

A count of zero means no serious adverse event was recorded in the listed group; it does not show that serious events are impossible or establish the absence of risk. General statistical principle: when groups are small, observing no events can still leave uncertainty about the underlying event frequency. The safety denominators differ from the analyzed denominators used for the primary endpoint, and the registry does not explain that difference.

The record separately reports other adverse events in the groups, but those counts should not be conflated with serious adverse events. The registry does not provide further detail about event severity, timing, relatedness, or how events were collected. The safety data are therefore descriptive and do not establish a comparative safety profile.

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

The posted results show fewer participants with a symptomatic, culture-proven urinary tract infection in the analyzed treatment arm than in the analyzed control arm. The estimated risk difference points toward a lower observed risk with D-mannose, but its confidence interval is broad and includes no difference and values in the opposite direction. The relative-risk and odds-ratio intervals likewise include their no-difference values. The evidence is therefore uncertain about the size and direction of the underlying difference.

This result does not establish that D-mannose prevents recurrent urinary tract infections, and it does not establish that D-mannose has no effect. The small analyzed groups, limited number of events, and unexplained differences between enrollment and outcome denominators constrain interpretation. The posted estimates describe the participants represented in the registry outcome results and the 90-day follow-up definition.

The randomized comparison applies specifically to postmenopausal participants with a history of recurrent urinary tract infection who were using vaginal estrogen therapy and were assigned to daily D-mannose powder or no additional intervention. The separate observational group had a different description and does not supply an equivalent randomized comparison. The results should not be generalized beyond these study conditions without further evidence.

The secondary outcomes and safety counts add descriptive context, but they do not eliminate uncertainty in the primary comparison. The registry does not report a complete statistical plan, missing-data approach, or multiplicity strategy. The planning illustrations are not observed evidence about efficacy. Overall, the posted record supports a cautious description of an imprecise comparison, not a definitive causal or clinical conclusion.

17. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a reliable estimate are not the same thing. The treatment arm had fewer participants with the primary event in the posted results, but the confidence interval remains wide and crosses the no-difference value. A point estimate alone can make a result appear more settled than the data justify; the interval conveys how much uncertainty remains.

It also highlights the importance of transparent participant accounting. The record gives overall enrollment, randomized allocation counts, the number said to have started study day 1, and smaller outcome denominators, but does not explain how those figures connect. Readers need a clear account of who was randomized, followed, and analyzed to judge how well the posted comparison reflects the randomized groups.

The study includes an observational group in addition to the randomized comparison. Keeping those designs distinct is essential: the randomized arms address the primary treatment-control question, while the observational data cannot by themselves isolate a treatment effect. The registry’s listing of multiple secondary outcomes also illustrates why prespecification and multiplicity reporting matter when interpreting secondary p-values.

Finally, the sample-size illustrations show how planning depends on the effect a future study aims to detect. The trial’s original sample-size justification is not reported, so the planning figures based on the observed effect cannot be taken as its design rationale. Together, these features make the record useful for understanding uncertainty, analysis populations, and the limits of interpretation in a small clinical trial.

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 affect interpretation. The registry reports randomized enrollment of 57 participants but primary outcome results for 19 treatment participants and 25 control participants. It also reports 44 participants starting study day 1 across all three groups and outcome data for 2 observational participants, without explaining how these figures relate. The amount and handling of missing outcome data are not reported in the registry record.

The primary comparison is based on a limited number of analyzed participants and events, and its confidence interval is broad. The registry does not provide detailed sponsor analyses, adjustment methods, or a full statistical analysis plan. It is not possible to determine whether covariate adjustment or a particular randomized analysis population was prespecified. The record does not report the original sample-size justification or interim-analysis procedures.

The study status is terminated, but the reason for termination is not reported in the registry record. It is also not reported whether termination affected recruitment, follow-up, or the planned analyses. The single-masking designation does not identify who was masked or explain how masking was maintained.

The observational arm is very limited in the posted outcome results and differs from the randomized population in vaginal estrogen use. It cannot be used as a direct randomized comparison. Multiple secondary outcomes are listed, but the record does not describe a hierarchy or multiplicity adjustment. Finally, the safety counts are descriptive; the record does not detail event collection, relatedness, or severity beyond the serious-event classification.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Nutraceutical Efficacy for rUTI — NCT03395288.
• Registry record last updated 2022-02-04; status last verified 2022-01.
• Results first posted 2022-02-04.
• 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

NCT03395288 is a terminated, randomized, controlled, parallel-group study sponsored by Washington University School of Medicine, with phase listed as phase 2 and phase 3. It examined daily D-mannose powder versus no additional intervention for 90 days among postmenopausal women with recurrent urinary tract infection using vaginal estrogen therapy. An observational group not using vaginal estrogen was also described.

The primary outcome was symptomatic, culture-proven urinary tract infection. The posted randomized-arm results were 6 events among 19 treatment participants and 12 among 25 controls, with a risk difference of -0.164 and a confidence interval from -0.451 to 0.122. The interval indicates substantial uncertainty. The registry does not explain the difference between randomized enrollment and the outcome denominators or report a complete analysis plan.

Secondary outcomes and serious adverse-event counts are also posted, but their interpretation is limited by small groups and unreported methods for missing data and multiplicity.