Phase II Study Efficacy and Safety of Two Dosing Regimens of MN-001 in Patients With Interstitial Cystitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase II Study Efficacy and Safety of Two Dosing Regimens of MN-001 in Patients With Interstitial Cystitis (NCT00295854), a randomized phase 2 study. The primary outcome is Number Subjects at Least "Moderately Improved" for Each Treatment Group in Patient Reported Global Response Assessment (GRA).

2. Clinical Question

The question focuses on participants’ own assessment of overall change, rather than a single symptom score. The GRA asked about change in pain, urgency, frequency, or the overall problem compared with the participant’s status before study medication. Its seven response categories ranged from markedly worse to markedly improved; the primary outcome counted responses at least moderately improved.

The comparison is therefore between the number of participants meeting that response threshold in each dosing group and the number in the placebo group. The primary endpoint was assessed at Week 8. A separate Week 4 GRA responder outcome is also listed as secondary, so it addresses an earlier assessment rather than replacing the primary question.

The registry reports outcome counts and recalculated unadjusted comparisons, but does not report a more detailed primary analysis plan or a defined analysis population. The results address the recorded GRA response threshold; they do not, by themselves, describe every aspect of symptom change or establish how participants who did not contribute outcome data were handled.

3. Trial Design

The registry identifies this as a phase II, randomized, double-blind, placebo-controlled, multicenter study with parallel groups. Masking is recorded as triple. The study compared MN-001 500 mg once daily, MN-001 500 mg twice daily, and placebo in patients with interstitial cystitis. The study summary describes 8 weeks of treatment. The listed start is 2005-05, primary completion is 2006-10, and the status is completed.

The registry lists enrollment of 296. The outcome records give separate denominators for each group, and those denominators are the relevant quantities for interpreting the posted endpoint results. The registry does not explain the relationship between the enrollment figure and the denominators contributing to each outcome. It also does not report how allocation was generated or concealed, the exact masking procedures, or whether masking was maintained throughout follow-up.

The primary endpoint was the number of participants reaching the GRA threshold of at least moderately improved at 8 weeks. A Week 4 GRA responder measure is listed as a secondary outcome. The record lists two outcome measures and reports no analyses in its analysis listing. The posted comparisons are unadjusted recalculations from the recorded summary counts, rather than reported sponsor analyses.

Random allocation and placebo comparison provide a framework for comparing the groups, but interpretation still depends on outcome measurement, missing data, and analysis choices. Details of the original sample-size justification, analysis populations, missing-data procedures, and any planned interim analyses are not reported in the registry record. These omissions limit what can be said about the intended statistical design beyond the study features explicitly recorded.

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: Eligible patients were randomized in a 1:1:1 ratio to receive 500 mg MN-001 twice daily (BID), 500 mg MN-001 once daily (QD), or placebo. Patients returned to the study center at Visit 3 (Day 28) and at Visit 4 (Week 8, Day 64) for safety and efficacy assessments. Patients were dispensed study drug at Baseline (Visit 2) and Visit 3.

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 Number Subjects at Least "Moderately Improved" for Each Treatment Group in Patient Reported Global Response Assessment (GRA), measured over 8 weeks.

The primary endpoint counts participants whose patient-reported GRA assessment indicated that their overall condition was at least moderately improved at Week 8. The GRA asked participants to compare their overall change in pain, urgency, frequency, or their overall problem with their status before taking the study medication. Responses used a seven-point scale: markedly worse, moderately worse, mildly worse, same, mildly improved, moderately improved, and markedly improved.

Counting participants who meet a defined improvement threshold turns those ordered response categories into a binary outcome: a participant either reaches the threshold or does not. The endpoint can therefore be compared as a response proportion in each randomized group, and the difference in those proportions can be expressed as a risk difference. A positive risk difference for an active-treatment group means a larger observed responder proportion than in placebo; a negative value means a smaller one.

This kind of patient-reported endpoint is used to capture participants’ overall view of change, which may encompass several symptoms rather than one isolated measure. The threshold also makes the outcome easier to interpret as a responder count. However, it does not retain all the detail in the original seven response categories. The posted counts cannot show how participants were distributed across each category, and the registry record does not report further information on the questionnaire’s validation, scoring procedures, or handling of incomplete assessments.

7. Results Posted in the Registry

• MN-001 500 mg qd: 32.6% (31/95) versus 29.4% (30/102) on control; risk difference 3.2 percentage points (95% CI -9.7 to 16.1), risk ratio 1.11 (0.73–1.68); unadjusted two-proportion z-test p = 0.625.
• MN-001 500 mg BID: 24.1% (26/108) versus 29.4% (30/102) on control; risk difference -5.3 percentage points (95% CI -17.3 to 6.6), risk ratio 0.82 (0.52–1.28); unadjusted two-proportion z-test p = 0.382.

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.

Number of Responders for GRA Assessment in Their Condition at Week 4.

• 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:
  • MN-001 500 mg qd: 20.7% (19/92) versus 12.1% (12/99) on control; risk difference 8.5 percentage points (95% CI -1.9 to 19.0), risk ratio 1.70 (0.88–3.31); unadjusted two-proportion z-test p = 0.110.
  • MN-001 500 mg BID: 24.8% (26/105) versus 12.1% (12/99) on control; risk difference 12.6 percentage points (95% CI 2.2 to 23.1), risk ratio 2.04 (1.09–3.82); unadjusted two-proportion z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MN-001 500 mg qd and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for MN-001 500 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a Week 4 GRA responder outcome as secondary. Its overall pattern differs from the Week 8 primary pattern: observed response proportions at Week 4 are higher in both MN-001 groups than in placebo, whereas the primary Week 8 comparisons do not show the same direction for both regimens. The Week 4 comparisons also differ in precision, with one interval including no difference and the other excluding it.

This earlier outcome adds information about the timing of the observed responses, but it does not replace the primary endpoint or establish that the Week 8 result would have been different with a later assessment. The registry does not report a longitudinal model or an analysis of change between the two assessments. The Week 4 and Week 8 outcomes should therefore be read as separate comparisons at their specified time points, not as a demonstrated trajectory.

Unadjusted secondary results carry less inferential weight when a statistical testing plan is unavailable. Testing multiple treatment comparisons and outcomes can increase the chance that at least one result appears notable by chance. The registry does not report whether any multiplicity adjustment was planned or applied. The Week 4 finding with an unadjusted p-value below 0.05 is consequently best regarded as a result that may merit attention, rather than as a definitive confirmation of a treatment effect.

The secondary outcome is also a responder count based on the GRA and shares the threshold-based limitations of the primary measure. It does not provide the full distribution of response categories or a detailed view of individual symptoms. The record does not report additional secondary analyses that could clarify whether the observed pattern is consistent across other measures. Taken together, the secondary results offer a signal that is distinct in timing and statistical status from the primary result, but they do not resolve the uncertainty in the Week 8 comparison.

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

• Number of Responders for GRA Assessment in Their Condition at Week 4.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because the GRA response is classified according to whether the participant reached the threshold of at least moderately improved. The posted counts and denominators permit an observed response proportion to be described for each group. A risk difference compares two such proportions by subtracting the placebo proportion from the treatment proportion. Positive values favor a greater observed response proportion in the treatment group; negative values indicate a smaller observed proportion. This is a descriptive contrast and does not, on its own, identify why the groups differ.

What does the confidence interval describe?

A confidence interval expresses the uncertainty around an estimated difference. For a risk difference, zero represents no difference between the compared response proportions. An interval that spans zero is compatible with no difference as well as with effects in either direction. An interval entirely on one side of zero indicates that the range of values compatible with the stated interval procedure does not include zero. The width also matters: a wider interval leaves more uncertainty about the size and direction of the underlying difference.

The posted primary comparisons have intervals spanning zero. The once-daily interval ranges from -0.097 to 0.162; the twice-daily interval ranges from -0.173 to 0.066. These ranges should be read alongside their point estimates, not as a guarantee that the true effect lies within the endpoints. The registry does not report the specific interval construction method or whether the original sponsor analysis used adjustment or covariates. The displayed comparisons are unadjusted recalculations from the posted summaries.

How should the p-values be read?

A p-value describes how unusual data at least as inconsistent with a specified no-difference model would be under that model and the assumptions of the calculation. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The primary recalculated p-values are 0.625 for once-daily treatment and 0.382 for twice-daily treatment. Read together with the intervals and counts, they do not provide a clear separation from placebo on the primary endpoint. They do not prove equivalence or establish that every possible effect is negligible.

The p-values are unadjusted. When several outcomes or treatment comparisons are examined, the chance of at least one apparently notable result can increase. A nominal p-value for one comparison does not account for that broader testing context. The registry record does not report a multiplicity strategy, so the Week 4 p-value should not be treated as if it were adjusted for the other outcome and treatment comparisons.

Why does over-dispersion matter?

Over-dispersion is a concern in analyses of count outcomes when the observed variability exceeds what a chosen model assumes. It can make standard errors too small and intervals too narrow if the model fails to allow for that extra variability. The primary outcome is recorded as participants meeting a binary responder threshold, rather than as a rate of recurrent events or a count of events per participant. Over-dispersion is therefore not the central issue in interpreting these posted responder comparisons. The registry does not report a model-based analysis or a dispersion assessment.

For binary outcomes, precision is influenced by the number of participants contributing endpoint data and by the response proportions. A group with few responders can yield substantial uncertainty in its estimated proportion and in a between-group contrast. Unequal group denominators can also affect the precision of comparisons. The reported confidence intervals capture uncertainty for each treatment-versus-placebo contrast, while the raw counts help readers understand how those contrasts arise.

What is and is not documented about the analysis?

The record lists zero analyses in its analysis listing and no reported secondary analyses. The displayed comparison statistics are simple unadjusted recalculations based on the posted summary statistics. The record does not report whether the primary analysis was intended to use an intention-to-treat, modified intention-to-treat, per-protocol, or other population. It does not report a missing-data method, adjustment for baseline characteristics, or a model for repeated measurements. Those details cannot be inferred from randomization or masking alone.

Randomization supports a comparison of assigned groups, but a complete interpretation also depends on who was included in each analysis and how missing outcomes were treated. If participants without Week 8 assessments were excluded, imputed, or classified in another way, each choice could affect the result. Because the registry does not state the approach, the posted denominators should be understood as the outcome-specific denominators recorded, not as proof of a particular analysis population or missing-data rule.

The same care applies to the response threshold. The endpoint counts participants in the two improvement categories at or beyond the threshold, but does not show the full distribution across all seven GRA options. A threshold-based comparison can be straightforward to interpret while concealing changes within the categories on either side of the cutoff. The registry record does not report a separate analysis of the ordinal response scale or the individual symptom questions.

11. Confidence Intervals and Precision

The Week 8 risk-difference estimate for once-daily MN-001 is 0.032, with a 95% confidence interval from -0.097 to 0.162. The interval crosses zero. It therefore includes the possibility of a lower responder proportion than placebo, no difference, and a higher responder proportion. The point estimate alone is not a precise description of the range of plausible differences.

For twice-daily MN-001, the Week 8 estimate is -0.053, with a 95% confidence interval from -0.173 to 0.066. This interval also crosses zero and permits values in both directions. Although its point estimate is negative, the range is not restricted to a lower responder proportion. The unadjusted p-values, 0.625 and 0.382, are consistent with the uncertainty reflected by these intervals.

The two primary intervals are not identical in width, and each allows a substantial range of risk differences. This means the summary data do not pin down the size or direction of either treatment contrast with high precision. Confidence intervals are more informative than a simple threshold reading of a p-value because they show the range of values that remains compatible with the estimate under the calculation’s assumptions. They still do not account for unreported design or analysis choices, such as missing-data handling or multiplicity.

At Week 4, the once-daily comparison has an interval from -0.019 to 0.190, while the twice-daily interval runs from 0.022 to 0.231. The former includes zero; the latter does not. The distinction concerns the uncertainty in those recalculated comparisons and does not resolve the less precise Week 8 primary result. The record’s lack of reported sponsor analyses and analysis-population details is an additional reason to interpret the precision as belonging to the posted unadjusted recalculations.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total numbers across groups and are not total event counts. The registry’s planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It sets the effect to detect as a stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the planned per-arm sample size under which the stated calculation would have an 80% chance of detecting the selected effect if that effect and the other planning assumptions held. The 90% power column uses a higher chance of detecting that effect under the calculation’s assumptions, which generally calls for more participants per arm. These are planning illustrations based on the observed effect, not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. This is because smaller differences are harder to distinguish from random variation than larger differences, all else equal. The curve communicates the same general relationship between the assumed effect and the planning requirement. It should not be interpreted as evidence that the trial was designed around those calculated sample sizes; the original design basis is not reported. The illustration also does not establish that the observed effect is a reliable estimate for a future study, particularly given the uncertainty in the endpoint comparisons.

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 = 0.294; treatment proportion p₁ = 0.326; average p̄ = 0.310.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6542 = 1.2822.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6538 = 0.5502.
4. n = (1.2822 + 0.5502)² / (0.0322)² = 3,238.9, rounded up to 3,239 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 <- 0.294117647058824                          # control proportion
p1 <- 0.326315789473684                          # 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(295854)
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 = 3,239 (80% power), 4,336 (90% power)
 75% of observed effect: n per arm = 5,718 (80% power), 7,654 (90% power)
 50% of observed effect: n per arm = 12,771 (80% power), 17,096 (90% power)
power.prop.test: 3238.9 
Simulated power at n = 3,239 per arm: 0.803 (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 one secondary outcome: the number of GRA responders at Week 4. The primary outcome is the Week 8 responder count. Each outcome includes comparisons of two MN-001 regimens with placebo, creating more than one opportunity for an apparently notable result. The registry does not report a prespecified multiplicity procedure, such as an adjustment to the significance threshold or a hierarchy for interpreting outcomes.

This matters because unadjusted testing treats each comparison separately. When several comparisons are examined, chance alone can produce a nominally small p-value more often than it would for a single prespecified test. The Week 4 twice-daily comparison has an unadjusted p-value of 0.02, but the record does not state whether it was designated as confirmatory or how it was to be interpreted alongside the other tests. Its result should be viewed in that context, not as an isolated decision rule.

The registry’s analysis listing reports zero analyses, and no reported secondary analyses are listed. The comparisons described in the results are recalculated from posted summary counts rather than being presented as sponsor analyses. The original statistical analysis plan, any planned interim analyses, and the original sample-size justification are not reported in the registry record. Their absence means the intended testing framework cannot be reconstructed from the posted endpoint summaries.

The analysis populations are also not reported. The record does not specify whether participants were analyzed according to randomized assignment, treatment received, or another population definition. It does not describe how missing Week 4 or Week 8 assessments were handled, whether participants with incomplete GRA responses were excluded, or whether any sensitivity analyses were performed. The listed outcome denominators identify the numbers associated with the posted counts but do not establish the rules used to select participants for analysis.

These omissions are important because exclusions and missing-data methods can affect both responder proportions and uncertainty. Without a stated plan, the recalculated comparisons should be treated as descriptive analyses of the registry’s recorded counts. They do not settle whether the sponsor’s prespecified analysis would use the same population, model, or inferential framework.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pregnancy (1.1%), infected epidermal cyst (1.0%).

The serious adverse event record lists 1 affected participant among 92 at risk in the once-daily group, 0 among 105 in the twice-daily group, and 1 among 99 in the placebo group. These are group-specific serious adverse event counts and denominators; they should not be combined or interpreted as a complete account of all safety outcomes. The registry also lists “Pregnancy” at 1.1% and “infected epidermal cyst” at 1.0% among the top serious adverse event terms.

The record does not report death counts. It lists other adverse events separately, but those counts are not serious adverse event counts. A low serious-event count in the posted record does not establish that no other safety concerns occurred, and a comparison of these counts alone does not account for event type, timing, severity, or exposure. The registry record does not provide enough detail to assess those aspects or to establish a causal relationship between treatment and an event.

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

The primary results describe the numbers meeting a patient-reported improvement threshold at Week 8 and the unadjusted differences between each MN-001 group and placebo. The estimates point in different directions for once-daily and twice-daily treatment, and both primary confidence intervals include zero. The posted data therefore leave uncertainty about the direction and size of the Week 8 treatment contrasts.

This does not mean that the groups have been shown to be equivalent. A result that is not clearly separated from zero can reflect a genuinely small difference, an imprecise estimate, or other features of the data and analysis. The intervals allow values on both sides of zero, so the results do not rule out either a lower or higher responder proportion relative to placebo. The record does not report an equivalence or noninferiority design.

The Week 4 secondary outcome has a more favorable observed pattern for the active groups, and the unadjusted twice-daily comparison has an interval excluding zero. That observation does not override the primary endpoint. It is secondary, comes from an earlier assessment, and is not accompanied by a reported multiplicity strategy or sponsor analysis. The record does not establish whether the Week 4 pattern persisted at Week 8.

The responder threshold also captures only part of the GRA information. It does not show how far participants moved along the seven response categories or which of pain, urgency, frequency, or overall problem drove their ratings. The outcome is a patient-reported assessment, and the record does not supply further information on validation or missing responses.

Accordingly, these registry results should be understood as comparisons of recorded responder counts, with uncertainty and limitations in the analysis documentation. They do not establish a general conclusion about every participant, every symptom, or every aspect of safety. The registry record does not report enough information to reconstruct the full analysis plan or to determine how incomplete outcome data were addressed.

17. Why This Trial Matters Statistically

This study illustrates why a trial’s primary endpoint and its timing matter. The Week 8 GRA responder outcome is the primary question, while the Week 4 measure is secondary. The observed pattern at the earlier assessment is not a substitute for the primary result, and the differences in timing should be preserved when interpreting either comparison.

It also illustrates the value of reading effect estimates and confidence intervals together. A p-value alone does not show the direction or range of an estimated difference. Here, the two primary point estimates point in opposite directions, and their intervals include zero and permit values in either direction. That combination communicates uncertainty more fully than a simple label of statistically significant or not statistically significant.

The registry includes raw responder counts and outcome-specific denominators, making it possible to understand the basis of the recalculated risk differences. At the same time, it lists no analyses and does not report the original analysis population, missing-data procedures, multiplicity plan, or sample-size justification. These gaps demonstrate why numerical results need to be considered alongside the completeness of the statistical record.

Finally, the planning illustration is distinct from the trial’s original design rationale. It explores participant requirements under stated assumptions based on observed effects, but the original sample-size assumptions are not reported. Treating those planning figures as evidence of observed power or as proof that the trial was adequately designed would confuse a retrospective illustration with the study’s documented design.

18. Limitations

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

The main limitation for interpreting the endpoint findings is the absence of a reported sponsor analysis. The registry lists no analyses, while the comparison statistics are unadjusted recalculations from the posted counts. The record does not state the original analysis model, the analysis population, or whether any baseline adjustment was planned. Therefore, the recalculated results may not represent the sponsor’s intended primary inferential analysis.

Handling of missing outcome data is not reported in the registry record. The outcome-specific denominators are smaller than the overall enrollment listed, but the record does not explain why participants are not represented in each outcome denominator or how missing assessments were handled. No particular reason or method should be inferred from those figures. Without the analysis population and missing-data details, it is difficult to assess how robust the responder comparisons are to incomplete follow-up.

The study uses a threshold on the GRA’s seven response categories. This makes a responder count easy to state but does not retain the full ordinal response distribution. The registry does not report category-level results, analyses of individual symptom domains, or additional details about questionnaire administration. The results therefore cannot describe the full range of patient-reported change captured by the GRA.

Multiplicity is another limitation. A primary outcome and a secondary Week 4 outcome are listed, each with comparisons across the treatment groups and placebo, but no adjustment or testing hierarchy is reported. The secondary p-value should consequently be interpreted cautiously. The original trial sample-size assumptions and justification are also not reported, so the retrospective planning figures cannot establish whether the trial was originally sized for the primary question.

Finally, the registry’s serious adverse event information is limited to group counts, denominators, and listed top terms. Death counts are not reported in the registry record. The posted safety figures do not supply the timing or fuller clinical context of events and should not be treated as a complete safety analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase II Study Efficacy and Safety of Two Dosing Regimens of MN-001 in Patients With Interstitial Cystitis — NCT00295854.
• Registry record last updated 2012-01-19; status last verified 2011-12.
• Results first posted 2012-01-19.
• 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

The registry record describes a completed, randomized, double-blind, placebo-controlled, multicenter phase II study of MN-001 in patients with interstitial cystitis. It compares 500 mg once daily and 500 mg twice daily with placebo over 8 weeks. The primary outcome is the number of participants at least moderately improved on the patient-reported GRA at Week 8; a Week 4 responder outcome is listed as secondary.

The primary posted counts are 31 of 95 for once-daily treatment, 26 of 108 for twice-daily treatment, and 30 of 102 for placebo. Unadjusted recalculated primary comparisons have confidence intervals that include zero. The Week 4 outcome has a different pattern, but no multiplicity plan is reported. The registry lists no analyses and does not report the original analysis populations, missing-data procedures, or sample-size justification. These details limit how fully the posted comparisons can be interpreted.