An Effectiveness and Safety Study for Levofloxacin in Chronic Prostatitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Effectiveness and Safety Study for Levofloxacin in Chronic Prostatitis (NCT00402688), a randomized phase 3 study. The primary outcome is Clinical Success.

2. Clinical Question

3. Trial Design

NCT00402688 is a completed, randomized, parallel-group Phase 3 study of levofloxacin for chronic prostatitis. The registry describes the study as multicenter and double-blind in its official title; its masking field records triple masking. The identities of the roles masked are not reported in the registry record. The registry lists enrollment as 242. The study start is recorded as 2006-11 and primary completion as 2008-03.

Participants were assigned to one of three daily oral regimens: levofloxacin 750 mg for 2 weeks followed by 2 weeks of placebo; levofloxacin 750 mg for 3 weeks followed by 1 week of placebo; or levofloxacin 500 mg for 4 weeks. The parallel design means that the posted groups represent separate treatment assignments rather than sequential treatment periods within the same participant. The registry does not report the allocation ratio or further details of sequence generation in the posted results.

The primary outcome was clinical success at the posttherapy visit, Study Day 33-36, in the mITT population. It was defined as cured or improved, based on resolution of signs and symptoms. The registry lists five secondary outcomes, including symptom relief, clinical success or failure at follow-up, and total NIH-CPSI score. It reports six outcome measures and two analyses. The detailed protocol, including the full analysis schedule and prespecified statistical methods, is not reported in the registry record.

Safety outcomes are also posted as counts. The record lists serious adverse events affecting 2 participants in the 750 mg for 2 weeks group, 1 in the 750 mg for 3 weeks group, and 0 in the 500 mg for 4 weeks group. Other adverse events affected 43, 42, and 38 participants, respectively. The numbers at risk for these safety summaries are not reported in the registry record, so these counts do not supply group-specific event rates.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent to Treat (mITT)

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 Clinical Success, measured over Posttherapy Visit (Study Day 33-36).

The primary endpoint is clinical success: the number of participants classified as cured or improved at the posttherapy visit, based on resolution of signs and symptoms. The specified assessment was at Study Day 33-36, and the analysis population was mITT. This endpoint turns a clinical assessment into a binary outcome for each participant: a person either met the stated success definition or did not.

A binary endpoint is useful for comparing the proportion of participants who reach a defined clinical state across treatment groups. The corresponding risk difference expresses the difference between those proportions in percentage-point terms when reported as a proportion. A positive estimate in a comparison means the first-named group had a higher observed success proportion than the comparison group; a negative estimate means it had a lower one. The endpoint therefore provides an interpretable measure of the observed group contrast, while the confidence interval describes uncertainty around that estimate.

The endpoint’s meaning depends on its definition and assessment timing. “Cured or improved” combines two categories, and the registry does not provide additional detail about the criteria separating them or the assessment procedure in the posted results. Clinical success at the posttherapy visit is not the same as sustained success over a longer period. The registry lists subsequent clinical success or failure outcomes among secondary outcomes, but those results are not included in the primary-outcome figures. Nor does this endpoint alone capture all aspects of safety, symptom burden, or participant experience.

7. Results Posted in the Registry

• Levofloxacin 750mg for 3 Weeks: 64.9% (48/74) versus 63.0% (46/73) on control; risk difference 1.9 percentage points (95% CI -13.7 to 17.4), risk ratio 1.03 (0.81–1.31); unadjusted two-proportion z-test p = 0.815.
• Levofloxacin 500mg for 4 Weeks: 69.3% (52/75) versus 63.0% (46/73) on control; risk difference 6.3 percentage points (95% CI -8.9 to 21.5), risk ratio 1.10 (0.87–1.39); unadjusted two-proportion z-test p = 0.416.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a risk difference express?

In general, a risk difference compares the probability of an event between two groups by subtracting one group’s probability from the other’s. For clinical success, the event is meeting the registry’s definition of cured or improved. The sign depends on which group is treated as the first group in the comparison. A positive value means a higher observed success proportion in that group; a negative value means a lower proportion. The measure is an absolute contrast, rather than a relative comparison.

The recalculated comparisons use the posted event counts and group sizes to estimate unadjusted risk differences. “Unadjusted” means the comparison is not presented as controlling for other variables. These estimates are descriptive contrasts between the posted groups, not adjusted estimates from a model. The registry’s own analyses are presented separately and should not be conflated with these recalculations.

What does the confidence interval add?

In general, a confidence interval describes the range of estimates compatible with the data under the method used to construct it. A narrower interval indicates greater precision; a wider interval indicates more uncertainty about the effect’s size. An interval that crosses zero for a risk difference includes no difference as one value compatible with the data. It may also include differences in either direction. That does not prove the groups are the same. It means the estimate does not pin down the contrast precisely enough to rule out the values within the interval.

The two recalculated 95% intervals both cross zero. Their widths show that the observed data leave substantial uncertainty about the size and direction of the underlying contrast. The endpoints should be read together with the point estimates: the point estimate is the single best estimate under the calculation, while the interval indicates how much uncertainty surrounds it. Neither an interval nor a p-value alone determines clinical importance.

How should the p-values be read?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it does not measure the probability that a result occurred “by chance.” The posted recalculated unadjusted p-values are 0.815 for the comparison between the two 750 mg regimens and 0.416 for the comparison of 500 mg for 4 weeks with 750 mg for 2 weeks. These values do not provide evidence of a statistically clear difference under a conventional null-difference test, but that is not evidence of equivalence.

The sponsor analyses are identified in the registry as non-inferiority or equivalence analyses, but the posted record does not include their method, p-values, or margin. In general, a non-inferiority analysis asks whether the data exclude a loss larger than a prespecified acceptable margin; an equivalence analysis asks whether the data exclude differences outside a prespecified range in both directions. These are not interchangeable with a conventional test for any difference. The registry record does not report the information needed to assess the margin-based decision rules.

Why does the analysis population matter?

The primary result is described as mITT. In general, an intention-to-treat approach seeks to preserve the comparison created by random assignment, while modified populations may apply additional rules. The registry does not report the precise inclusion and exclusion rules used for this mITT analysis. Therefore, the group counts and risk differences should be understood as results for the named analysis population, not automatically as results for every randomized participant.

Missing outcome handling can affect a binary endpoint if some participants lack an assessment. The registry record does not report the amount of missing primary-outcome data or the method used to handle it. Without those details, it is not possible to judge whether missingness could materially influence the comparison. Similarly, the statistical analysis plan and any covariate adjustments are not reported in the registry record.

What do the safety counts show?

The registry lists serious adverse event counts and other adverse event counts by group, but the denominators at risk are not reported. In general, counts alone do not allow a direct comparison of event rates when the numbers observed or followed may differ. The serious adverse event counts are 2, 1, and 0 across the three listed groups; the other adverse event counts are 43, 42, and 38. The record also names serious event terms at 1.2% each: Syncope, Coronary Artery Disorder, Depression, Hallucination, and Suicidal Ideation. These posted summaries do not provide enough information to estimate comparative safety risks or establish that an event was caused by treatment.

In general, over-dispersion is a concern when event counts vary more than a model assumes. It is particularly relevant for count outcomes and clustered or repeated observations. The primary endpoint is binary, with one clinical-success classification per participant in the reported analysis. The registry does not report a model for the primary analysis, so it is not possible to say whether over-dispersion was assessed or relevant to the sponsor’s method. No particular model should be inferred from the posted values alone.

10. Confidence Intervals and Precision

The recalculated risk difference for 750 mg for 3 weeks compared with 750 mg for 2 weeks is 0.018. Its 95% confidence interval runs from -0.137 to 0.174. This interval crosses zero, so it is compatible with no difference as well as with a lower or higher clinical-success proportion in the 3-week group. The point estimate is not precise enough to settle the direction or size of the contrast.

For 500 mg for 4 weeks compared with 750 mg for 2 weeks, the recalculated risk difference is 0.063, with a 95% confidence interval from -0.089 to 0.215. This interval also crosses zero and covers differences on both sides of zero. The positive point estimate is therefore not a conclusive finding that the 4-week regimen has a higher success proportion.

In general, confidence intervals reflect sampling uncertainty under the calculation method; they do not account automatically for every possible source of bias, missing data, or design limitation. The intervals are based on the posted group summaries and are unadjusted. They should not be interpreted as a guarantee that the true effect lies within the stated limits, nor as a range of individual treatment responses. They describe uncertainty in a group-level contrast.

The sponsor’s posted interval for the 2-week 750 mg group compared with the 4-week 500 mg group is -0.089 to 0.215, around a reported risk difference of 0.063. For the 3-week 750 mg group compared with the 4-week 500 mg group, the interval is -0.106 to 0.195, around a reported risk difference of 0.045. The registry does not report the margin used for its non-inferiority or equivalence analyses. Consequently, the interval endpoints cannot be judged against a prespecified margin using the registry record alone.

Precision is not the same as clinical importance. Whether a difference of a particular size would matter clinically depends on context and criteria not reported in the registry record. The posted estimates support cautious description of the observed comparisons, not a definitive ranking of the regimens.

11. 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 stated as participants per arm for the two-group comparisons, not total participants and not total events. Each row illustrates a target effect defined as a fraction of the observed effect: 100%, 75%, or 50% of that observed effect. The figures are planning illustrations calculated from the observed effect, not the trial’s original design assumptions. The registry record does not report the original sample-size justification or the assumptions used to design the trial.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The 80% power column gives the approximate participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding planning number for a 90% chance.

Smaller effects require more participants to distinguish them from random variation under the same assumptions. This is why planning for 75% or 50% of the observed effect requires larger per-arm figures than planning for the full observed effect. These illustrations depend on the observed effect, which is uncertain, and should not be treated as a recommended design without separate scientific and statistical justification.

This is not observed power. It is a prospective planning illustration based on the observed effect and stated assumptions, not a measure of how likely the completed trial was to detect an effect after its results were known. The displayed curve should be read as a visual representation of the same planning relationship: more participants are needed to target smaller effects at a chosen power level. No time-to-event outcome is involved in these calculations; the planning figures are participants per arm.

12. 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 = 0.630; treatment proportion p₁ = 0.649; average p̄ = 0.639.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6791 = 1.3310.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6789 = 0.5714.
4. n = (1.3310 + 0.5714)² / (0.0185)² = 10,560.9, rounded up to 10,561 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 <- 0.63013698630137                          # control proportion
p1 <- 0.648648648648649                          # 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(402688)
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 = 10,561 (80% power), 14,138 (90% power)
 75% of observed effect: n per arm = 18,828 (80% power), 25,205 (90% power)
 50% of observed effect: n per arm = 42,480 (80% power), 56,868 (90% power)
power.prop.test: 10560.9 
Simulated power at n = 10,561 per arm: 0.796 (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.

13. Analyses Reported by the Sponsor

The registry’s sponsor-reported analyses are distinct from the recalculated unadjusted comparisons. For the 2-week 750 mg group compared with the 4-week 500 mg group, the sponsor reports a risk difference of 0.063 and a 95% confidence interval from -0.089 to 0.215. The recalculated estimate for that same contrast is 0.063, with a 95% confidence interval from -0.089 to 0.215. These values are close, with small differences in displayed rounding.

For the 3-week 750 mg group compared with the 4-week 500 mg group, the sponsor reports a risk difference of 0.045 and a 95% confidence interval from -0.106 to 0.195. The recalculation displayed for the 3-week group instead compares it with the 2-week 750 mg group, yielding 0.018 with a 95% confidence interval from -0.137 to 0.174. Those are different comparisons, so their estimates should not be treated as competing calculations of the same contrast.

The registry labels the sponsor analyses as non-inferiority or equivalence analyses but does not report their method, p-values, or decision margin. The sponsor’s own analysis takes precedence for interpreting its reported analysis. The recalculations are simple unadjusted comparisons from the posted summary statistics and do not replace that analysis. Since the posted record does not include the margin or full method, the formal basis for a non-inferiority or equivalence conclusion cannot be reconstructed from the reported values alone.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists five secondary outcomes, including symptom relief, clinical success or failure at follow-up, and total NIH-CPSI score. It also reports six outcome measures and two analyses. When several outcomes or comparisons are examined, the chance of observing at least one apparently notable result can increase. In general, multiplicity procedures can control that risk, but the registry record does not report whether any such adjustment was planned or used. No adjustment should be assumed from the posted results.

The primary outcome is clearly identified as clinical success at the posttherapy visit, which helps distinguish it from the secondary outcomes. However, the full statistical analysis plan, any hierarchy among endpoints, and any multiplicity strategy are not reported in the registry record. The posted analyses therefore do not establish how all outcome comparisons were interpreted together or whether the reported analyses were prespecified in the same form.

The record identifies the primary analysis population as mITT but does not report the specific mITT definition or the numbers excluded from that analysis. It also does not report missing primary-outcome counts or the method used to handle missing assessments. In general, missing outcomes can alter a group comparison, particularly if the reasons for missingness differ between groups or relate to the outcome. Without those details, the sensitivity of the result to missing-data assumptions cannot be assessed from the posted record.

The registry does not report whether interim analyses were conducted, whether there were prespecified stopping rules, or whether any adjustments for interim looks were used. The protocol and detailed analysis plan are not reported in the registry record. These omissions limit assessment of how the posted estimates relate to the complete planned analysis, but they do not change the arithmetic meaning of the posted counts and risk differences.

Safety summaries also have missing denominator information: the numbers at risk for the adverse-event counts are not reported in the registry record. As a result, those counts cannot be converted into comparable group-specific risks using the posted information alone. Death counts are not reported in the registry record.

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

The results describe clinical success at one specified posttherapy assessment among participants in the mITT analysis. The posted counts are 46 of 73 for levofloxacin 750 mg for 2 weeks, 48 of 74 for 750 mg for 3 weeks, and 52 of 75 for 500 mg for 4 weeks. The recalculated comparisons have confidence intervals that include no difference and permit values on either side of zero. The data therefore do not precisely determine the direction or size of the between-group differences.

These results do not demonstrate that the regimens are equivalent. A non-significant conventional comparison is not an equivalence test, and formal non-inferiority or equivalence interpretation depends on the prespecified margin and analysis method. Although the registry labels two sponsor analyses as non-inferiority or equivalence analyses, the margin and method are not reported in the registry record. That prevents independent assessment of the decision rule from the posted results.

The results also do not prove that the regimens have identical safety profiles. Serious and other adverse event counts are posted, but the numbers at risk are not reported. The listed serious event terms and percentages do not, on their own, show whether events were caused by treatment or whether the groups differed in safety risk.

The endpoint reflects a combined cured-or-improved classification at Study Day 33-36. It does not establish the durability of success over longer follow-up, the separate frequency of cure and improvement, or every aspect of symptoms and quality of life. Secondary outcomes are listed in the registry, but their results are not included in the primary-outcome data. Generalization beyond the enrolled study population also depends on eligibility and participant characteristics that are not reported in the registry record.

In short, the posted primary results support a careful account of observed counts and uncertain group contrasts. They do not support medical advice or a definitive conclusion that one regimen should be selected over another.

16. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be read without its uncertainty interval. The observed primary-outcome counts differ across the three regimen groups, but the recalculated risk-difference intervals include zero and span possible contrasts in both directions. The visual and numerical impression of a difference in raw counts is not sufficient to establish a reliable treatment contrast.

It also demonstrates that the comparator matters. The recalculated 3-week versus 2-week comparison is not the same question as the sponsor-reported 3-week versus 4-week comparison. Estimates can only be compared directly when they refer to the same outcome, population, and group contrast. Clear naming of both arms prevents a numerical result from being assigned to the wrong clinical question.

The registry’s non-inferiority or equivalence classification raises another important statistical distinction. Failure to identify a conventional difference does not establish that treatments are sufficiently similar. A margin-based analysis needs a defined threshold and a method that evaluates the confidence interval against it. Those details are not reported in the registry record, so the classification cannot be fully evaluated from the posted results alone.

Finally, the safety counts show why denominators and analysis details matter. Counts without numbers at risk do not provide comparable event rates. The primary outcome also depends on the mITT definition and missing-data handling, neither of which is fully described in the record. These are not technical footnotes: they determine what population and uncertainty the estimates represent. The trial is a useful example of reading randomized comparisons alongside their limits rather than treating a single estimate as a complete answer.

17. 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 posted primary outcome is available for the mITT population, but the registry record does not report the specific rules defining that population. It is therefore unclear from the posted results how it relates to all randomized participants. The record also does not report the amount of missing primary-outcome data or how missing assessments were handled, limiting assessment of possible bias from incomplete outcome ascertainment.

The primary endpoint combines “cured” and “improved,” and the registry record does not provide the detailed criteria or assessment process used to classify participants. The outcome is measured at the posttherapy visit on Study Day 33-36; the primary result alone does not describe longer-term durability. Although secondary follow-up outcomes are listed, their results are not part of the posted primary-outcome figures discussed in this analysis.

The sponsor analyses are labeled as non-inferiority or equivalence analyses, but the registry record does not report their analysis method, p-values, or margin. That omission prevents readers from checking the formal criterion for those analyses. The statistical analysis plan, multiplicity strategy, interim-analysis information, and original sample-size assumptions are also not reported in the registry record.

For safety, the posted counts do not include numbers at risk, preventing direct comparison of group-specific rates. Death counts are not reported in the registry record. The listed serious adverse-event terms and percentages should be interpreted as registry summaries, not as evidence of causation or of comparative risk.

Finally, the recalculated estimates are unadjusted summaries based on the posted counts and group sizes. They do not account for unreported covariates, possible protocol deviations, missing data, or other features of the original analysis. They are useful for describing the posted data but do not replace the sponsor’s analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: An Effectiveness and Safety Study for Levofloxacin in Chronic Prostatitis — NCT00402688.
• Registry record last updated 2013-09-13; status last verified 2013-09.
• Results first posted 2009-07-16.
• 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.

21. Record Summary

NCT00402688 is a completed, randomized, parallel-group Phase 3 study of levofloxacin for chronic prostatitis, with enrollment recorded as 242. The three regimens were 750 mg daily for 2 weeks followed by placebo, 750 mg daily for 3 weeks followed by placebo, and 500 mg daily for 4 weeks. The registry describes the study as multicenter and its masking field as triple.

The primary endpoint was clinical success, defined as cured or improved based on resolution of signs and symptoms at the posttherapy visit on Study Day 33-36. The mITT counts were 46 of 73, 48 of 74, and 52 of 75 across the respective groups. Recalculated risk-difference intervals include zero for both unadjusted comparisons. The registry also posts sponsor analyses classified as non-inferiority or equivalence, but the method and margin are not reported in the registry record.

Safety counts are posted without numbers at risk. Missing-data handling, the detailed analysis plan, and the trial’s original sample-size assumptions are not reported in the registry record.