Gemcitabine Hydrochloride and Cisplatin With or Without Bevacizumab in Treating Patients With Advanced Urinary Tract Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Gemcitabine Hydrochloride and Cisplatin With or Without Bevacizumab in Treating Patients With Advanced Urinary Tract Cancer (NCT00942331), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

The clinical comparison is between two regimens that share gemcitabine and cisplatin; the randomized difference is the addition of bevacizumab rather than placebo. Double masking and parallel assignment are recorded. The primary outcome is time-to-event, so the comparison concerns the pattern of deaths over follow-up, not simply the number of participants alive at a single fixed visit. Other registered outcomes include progression-free survival, objective response, and grade 3 or higher toxicity. The registry record does not report a posted progression-free survival result.

3. Trial Design

This was a randomized, double-blind, parallel-group phase III study sponsored by the National Cancer Institute. The registry lists enrollment of 506 participants and a completed status. The recorded start date is 2009-07-15, and the primary completion date is 2018-11-02. The treatment comparison assigned participants to gemcitabine and cisplatin with either bevacizumab or placebo.

Both arms used the same chemotherapy backbone. Gemcitabine hydrochloride was administered intravenously on days 1 and 8, while cisplatin and the blinded bevacizumab or placebo infusion were administered on day 1. The treatment description specifies cycles every 21 days for 6 cycles if disease had not progressed and toxicity remained acceptable, followed by continued bevacizumab or placebo. The registry describes intravenous administration and infusion durations. It does not report adherence, dose intensity, or the extent to which participants completed the planned regimen.

The primary outcome was overall survival, defined as time from randomization to death from any cause. Its timeframe was assessed up to 7 years, and the stated population was the intent-to-treat analysis population. The registry describes median survival estimates using the Kaplan-Meier estimator and a primary comparison using a stratified log-rank statistic. It identifies the stratification factors as presence of visceral metastases and prior chemotherapy, each classified as yes or no. The registry also describes use of a proportional hazards model to assess treatment and patient characteristics as predictors of survival.

Although the outcome description provides some planned analysis details, the registry record does not report the original sample-size justification, planned event target, or details of any interim analyses. Further information on treatment allocation procedures and the operational details of masking is not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat (ITT) analysis population

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 Overall Survival (OS), measured over From date of randomization to date of death due to any cause, assessed up to 7 years.

Overall survival measures the time from randomization until death from any cause. It is a time-to-event endpoint: each participant contributes information about survival duration, and participants who have not had the event by the end of their observed follow-up contribute censored information rather than being treated as if their eventual outcome were known. The registry describes the endpoint as assessed up to 7 years.

Overall survival is used because it captures a direct and unambiguous event and does not require deciding whether a change in a scan or a symptom represents progression. Because follow-up can vary and not every participant experiences the event during observation, a survival analysis can use available follow-up information rather than reducing the outcome to a simple alive-or-dead count at one time point. The Kaplan-Meier estimator, named in the registry description, estimates the survival curve while accounting for censoring.

The median is the point on the estimated survival distribution at which the estimated probability of remaining alive reaches one half. It provides a compact summary of the survival-time distribution, but it does not describe the entire curve. A hazard ratio instead compares the relative event rates over follow-up under the assumptions of the chosen model. These summaries answer related but different questions, so the medians, their confidence intervals, and the hazard ratio should be read together rather than treated as interchangeable.

Overall survival is clinically interpretable, but it does not by itself identify the biological reason for a difference or establish which component of a regimen caused it. The randomized comparison estimates the contrast between the complete assigned regimens.

7. Results Posted in the Registry

• Arm II (GCB) vs Arm I (GCP): hazard ratio 0.87 (95% CI 0.72–1.06), reported p = 0.171 (as reported in the registry).

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.

Objective Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm I (GCP): 0.5% (1/209) versus 0.5% (1/213) on control; risk difference 0.0 percentage points (95% CI -1.3 to 1.3), risk ratio 1.02 (0.06–16.19); unadjusted two-proportion z-test p = 0.989.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I (GCP) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Experiencing Grade 3+ Toxicity

• 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:
  • Arm I (GCP): 70.3% (163/232) versus 77.2% (183/237) on control; risk difference -7.0 percentage points (95% CI -14.9 to 1.0), risk ratio 0.91 (0.82–1.01); unadjusted two-proportion z-test p = 0.087.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm I (GCP) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of the treatment comparison: progression-free survival, objective response, and grade 3 or higher toxicity. Their measures and analysis populations differ, so their findings should not be treated as interchangeable evidence about overall survival. Progression-free survival is named in the registry, but its result is not reported in the registry record.

The posted objective-response estimates are close between arms. The unadjusted comparison does not provide evidence of a clear difference. For grade 3 or higher toxicity, the posted counts and unadjusted comparison indicate a numerical difference, but the comparison remains uncertain and does not meet the conventional 0.05 threshold. These broad patterns do not overturn or resolve the primary overall-survival result. They provide additional descriptive context, rather than a confirmed explanation for the survival estimate.

The registry record does not list sponsor-reported inferential analyses for the posted objective-response and toxicity results. Unadjusted calculations may be useful for orientation, but they do not account for the full planned analysis or any possible covariates. They should therefore carry less weight than the sponsor's designated primary analysis.

There are multiple secondary outcomes, and testing several outcomes can raise the chance of at least one apparently noteworthy result by chance. The registry record does not report a multiplicity adjustment or a hierarchy specifying which secondary comparisons should be treated as confirmatory. Without such information, a nominal unadjusted finding should be considered exploratory. The primary endpoint remains the clearest basis for interpreting the trial's main statistical question, while secondary results can suggest questions for further investigation rather than establish them.

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

• Progression-free Survival (PFS)
• Objective Response
• Number of Patients Experiencing Grade 3+ Toxicity

9. Statistical Interpretation

10. Statistical Methods Explained

Overall survival is a time-to-event outcome because the endpoint records the time until death, rather than only whether death occurred within a fixed interval. Participants can have different lengths of follow-up. Some may still be alive at their last recorded observation, so their survival time is censored: the analysis knows they survived at least until that observation, but not their subsequent survival time. The registry record does not describe the censoring rules or how loss to follow-up was handled.

What does a Kaplan-Meier median summarize?

The Kaplan-Meier estimator builds an estimated survival curve from the observed event times while accounting for censoring. The median survival is the time at which that estimated curve reaches one half. It is a useful summary of the timing of events, but it is only one feature of the curve. Two groups can have similar medians while having different patterns at other parts of follow-up, or different medians while having substantial uncertainty. The confidence intervals around the posted medians convey some of that uncertainty.

A median is not the average survival time, nor does it state how long any individual participant will live. It also does not give a direct measure of the probability of being alive at every time point. The registry reports the medians and their confidence intervals but does not provide survival probabilities at specific time points in the listed details.

What does a hazard ratio compare?

A hazard is the instantaneous event rate among participants who have not yet experienced the event, conditional on remaining under observation. A hazard ratio compares hazards between groups over follow-up. The posted hazard ratio of 0.87 compares Arm II with Arm I; the reported 95% confidence interval is 0.72 to 1.06. A value of 1 represents equal hazards in the comparison. A value below 1 points toward a lower estimated hazard in the first-named arm, while a value above 1 points toward a higher estimated hazard.

A hazard ratio is not a ratio of median survival times, and it is not a direct percentage change in survival time. Its interpretation as a single summary is most straightforward when the proportional hazards assumption is reasonable—that is, when the relative hazards are sufficiently stable over time. The registry describes use of a proportional hazards model, but does not report an assessment of that assumption or a plot of time-varying effects. The registry record does not report whether an alternative summary was planned if proportional hazards did not hold.

Why use a log-rank comparison?

The log-rank test compares the observed event experience between groups across event times, taking account of the numbers still at risk. The primary outcome description specifies a stratified log-rank statistic, with strata defined by presence of visceral metastases and prior chemotherapy. Stratification can account for those baseline categories in the comparison. The registry's posted analysis labels its method as Log Rank and reports a hazard ratio, but does not provide further detail about stratification in that posted result.

The registry outcome description also states that a proportional hazards model would be used to assess treatment while adjusting for patient characteristics, stratification variables, and other important covariates. The listed result does not include a separate adjusted hazard ratio, covariate list, or model diagnostics. Those results are not reported in the registry record.

What does a confidence interval tell the reader?

A confidence interval presents a range of estimates compatible with the observed data under the method's assumptions. It communicates uncertainty more fully than a point estimate alone. For the hazard ratio, the interval includes 1, so the data do not exclude equal hazards at the conventional confidence level. The interval also includes values below and above 1, so it does not pin down the direction with high precision. Confidence intervals do not assign a probability that the true value lies within the particular interval after the data have been observed; they describe the behavior of the method over repeated use under its assumptions.

The reported p-value addresses how unusual the data would be under a specified null hypothesis and analysis framework. It does not measure the probability that the null hypothesis is true, the size of an effect, or the clinical importance of an estimate. Here the p-value is above 0.05, consistent with the interval including the no-difference value. Statistical non-significance does not establish equivalence, since equivalence requires an explicitly defined margin and an analysis designed to evaluate it. Such a margin is not reported in the registry record.

Why do survival analyses need assumptions?

Kaplan-Meier and log-rank methods rely on assumptions about how censoring relates to the outcome. In broad terms, censoring should not systematically hide different outcome experiences in a way that distorts the group comparison. The proportional hazards model also has its own assumptions about the relative hazards. General statistical practice calls for checking these assumptions and describing important departures, but the registry record does not report such diagnostics. The analysis should therefore be read as the reported result, with the model assumptions in mind rather than as an assumption-free measurement.

The comparison is randomized and double-blind according to the registry. Randomization is intended to make treatment groups comparable on average at baseline, while masking can reduce some forms of bias in care and outcome assessment. The record does not provide enough detail to assess the implementation of those processes or whether masking remained intact.

11. Confidence Intervals and Precision

The confidence intervals show that the estimates are not exact. The median overall survival estimate in Arm II is 14.5 months, with a 95% confidence interval from 13.5 to 16.2 months. In Arm I, the estimate is 14.3 months, with a 95% confidence interval from 12.1 to 16.2 months. The overlap indicates that the individual median estimates are not sharply separated by their reported uncertainty. However, comparing overlap between separate confidence intervals is not a substitute for the formal between-arm analysis.

The hazard ratio provides the direct relative comparison. Its estimate is 0.87, and its 95% confidence interval runs from 0.72 to 1.06. Since the interval includes 1, it is compatible with no relative hazard difference as well as with effects in either direction. The interval's lower and upper limits also show that the estimate is not precise enough to establish a narrow range of plausible relative effects. The reported p-value is above 0.05, in keeping with that uncertainty.

Precision depends on information in the analysis, including the number and timing of events and the amount of follow-up. Enrollment alone does not show how much information was available for the final survival comparison. The registry record does not report the total number of deaths used in the primary analysis or detailed follow-up distributions. The counts listed with safety results are not a substitute for the number of events in the overall-survival analysis.

A confidence interval is not a guarantee that the true effect lies inside its bounds. It is an uncertainty summary under the analysis assumptions. Nor does a confidence interval by itself answer whether an effect would be clinically important; that depends on the range of effects that matters in context, which is not defined in the registry record. The findings support a cautious reading: the point estimate favors Arm II numerically, but uncertainty includes the no-difference value and does not establish a definitive survival advantage.

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 illustrations are based on the observed effect and use a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. For the time-to-event outcome, the entries are total events, calculated using the Schoenfeld approach; they are not participant counts per arm. For the other outcomes, the entries are participants per arm. The registry record does not report the trial's original design assumptions, so these illustrations should not be mistaken for the enrollment target or event target used when the trial was planned.

The 80% power column describes the number of events or participants that a hypothetical study would need, under the stated assumptions, to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column describes the corresponding requirement for a 90% chance. These are planning probabilities under an assumed effect and analysis model; they do not say how likely the current trial was to produce a significant result.

The rows use 100%, 75%, and 50% of the observed effect as alternative planning targets. Smaller target effects require more information to detect reliably, so the required event or participant counts increase as the assumed effect becomes smaller. This pattern reflects a general statistical principle: subtle differences are harder to distinguish from random variation than larger differences.

These values are not observed power. They are prospective planning illustrations calculated from the observed effect, not a retrospective measure of whether the completed trial was adequately powered. Interpreting them also requires attention to the observed estimate's uncertainty: a planning calculation based on a noisy observed effect can yield unstable requirements. The table's units matter, and the time-to-event figures must not be read as participants per arm.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.870, so ln(HR) = -0.1393.
2. d = 4 × (1.96 + 0.842)² / [ln(0.870)]² = 1,618.8, rounded up to 1,619 events in total 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
hr <- 0.87                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(942331)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 1,619 (80% power), 2,168 (90% power)
 75% of observed effect: events = 2,878 (80% power), 3,853 (90% power)
 50% of observed effect: events = 6,476 (80% power), 8,669 (90% power)
Simulated power with 1,619 events: 0.805 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 2,898 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 506 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 14.3          # control-arm median, months (converted from the posted unit)
hr          <- 0.87          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
     Analysis               Value Efficacy
    IA 1: 33%                   Z   3.7103
      N: 2322         p (1-sided)   0.0001
  Events: 731        ~HR at bound   0.7599
    Month: 19    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.87   0.0338
    IA 2: 67%                   Z   2.5114
      N: 2898         p (1-sided)   0.0060
 Events: 1461        ~HR at bound   0.8769
    Month: 31    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.87   0.5603
        Final                   Z   1.9930
      N: 2898         p (1-sided)   0.0231
 Events: 2192        ~HR at bound   0.9184
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.87   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The posted primary comparison reports a hazard ratio of 0.87 for Arm II versus Arm I, with a 95% confidence interval from 0.72 to 1.06 and a p-value of 0.171. The analysis is identified as Log Rank. The registry's primary outcome description specifies a stratified log-rank statistic as the primary analysis and describes a proportional hazards model as an additional analysis. The posted result does not give a separate adjusted model estimate.

The recalculated presentation uses the sponsor-reported hazard ratio for this time-to-event outcome. It does not replace or independently re-estimate the sponsor's survival analysis from arm-level summaries. The registry record does not identify a discrepancy between the posted and recalculated presentation. Accordingly, the sponsor's reported analysis is the relevant inferential result for overall survival.

The confidence interval includes 1, and the reported p-value is above 0.05. These features indicate that the posted analysis does not establish a statistically significant difference at the conventional threshold. They do not prove that the two regimens are equivalent, and the interval still allows a range of effects. The medians are descriptive summaries; the sponsor-reported hazard ratio and log-rank analysis address the between-group time-to-event comparison.

The registry does not provide the underlying event-time data, analysis code, or complete model output. A reader therefore cannot use the posted summary alone to verify every aspect of the sponsor's analysis or reproduce its adjustment and stratification details.

16. Multiplicity, Missing Data and Analysis Populations

The primary endpoint description identifies the intent-to-treat population and names a stratified log-rank statistic as the primary comparison. It also describes a proportional hazards model for adjustment. The registry record does not report the original statistical analysis plan, the complete covariate set, or whether the posted log-rank result implemented the stated stratification factors. It also does not report any interim analyses or stopping rules.

Several outcomes are registered, including overall survival, progression-free survival, objective response, and grade 3 or higher toxicity. The record does not describe a multiplicity adjustment, a testing hierarchy, or a procedure for controlling the overall type I error across multiple outcomes. This matters because interpreting many tests at once increases the opportunity for chance findings. Unadjusted secondary comparisons should not be treated as if they had the same confirmatory status as a prespecified primary endpoint.

The primary endpoint uses an intent-to-treat analysis population, which generally means participants are analyzed according to randomized assignment. That approach preserves the randomized comparison, subject to the analysis details. However, the registry record does not explain how missing outcome information, withdrawals, loss to follow-up, or treatment changes were handled. It does not report censoring rules, the amount of missing data, or sensitivity analyses.

Objective response is reported for 213 participants in Arm II and 209 in Arm I, while the toxicity result is reported for 237 participants in Arm II and 232 in Arm I. The registry does not explain the differences between these analysis counts and the primary enrollment or specify the eligibility rules for each endpoint analysis. The primary outcome description identifies the intent-to-treat population, but comparable population details for the secondary results are not reported in the registry record.

These omissions do not invalidate the posted results, but they limit assessment of how fully the analyses followed the planned statistical approach and how sensitive results may be to missingness or analysis choices.

17. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hemoglobin decreased (30.4%), fatigue (30.0%), platelet count decreased (21.1%), creatinine increased (16.8%), neutrophil count decreased (13.1%).

The registry reports counts for serious adverse events and other adverse events among participants at risk in each arm. In Arm II, 95 of 237 participants at risk were recorded as having a serious adverse event; in Arm I, 87 of 232 were recorded. Other adverse events were reported for 215 of 237 participants in Arm II and 205 of 232 in Arm I. These are counts among the listed at-risk populations, not estimates of event rates per unit of follow-up.

The most frequent serious adverse event terms listed across the posted results include hemoglobin decreased at 30.4%, fatigue at 30.0%, platelet count decreased at 21.1%, creatinine increased at 16.8%, neutrophil count decreased at 13.1%, and vomiting at 12.5%. The registry record does not specify in this summary whether each listed percentage is calculated using the same denominator or how events were attributed when participants experienced more than one event.

Safety counts describe what was recorded; they do not by themselves establish that one regimen caused more harm than the other. The registry record does not provide a formal between-arm safety analysis, exposure-adjusted rates, or event timing. A serious adverse event is not identical to a grade 3 or higher toxicity outcome, so these measures should be read separately. Death counts are also reported, but they should not be interpreted as a safety comparison without the corresponding analysis context.

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

The results answer a specific question: in this randomized comparison, what was the overall-survival experience with gemcitabine and cisplatin plus bevacizumab compared with gemcitabine and cisplatin plus placebo? The posted median estimates are similar, and the hazard ratio points numerically toward lower hazards in the bevacizumab arm. However, the confidence interval includes 1 and the reported p-value is above 0.05. The data therefore do not establish a statistically significant overall-survival difference by the reported analysis.

That conclusion is not the same as showing that the regimens are equivalent. A non-significant result can arise when the true effect is small, when the estimate is imprecise, or when the data do not distinguish the observed effect from chance variation. Equivalence or non-inferiority requires a prespecified margin and a suitable analysis; such a margin is not reported in the registry record. The confidence interval communicates a range of effects compatible with the analysis rather than a definitive statement that the effect is zero.

The trial estimates the contrast between the assigned regimens in its enrolled population. It does not isolate the biological contribution of each drug independently, and the primary outcome does not show why any difference might occur. The registered population includes several advanced or metastatic urinary tract cancer descriptions. The record does not provide enough information to determine how the result varies across every listed disease site or clinical subgroup.

The secondary outcomes may add context, but the registry does not report progression-free survival results, and the objective-response and toxicity comparisons are not presented as sponsor-reported confirmatory analyses. They should not be used to make a stronger claim than the primary analysis supports. The findings also do not establish results for other populations, treatment schedules, or comparisons that were not studied.

In short, the posted evidence is compatible with a range of relative survival effects and does not establish a clear difference between the two assigned regimens. It also does not prove that their effects are identical.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should be read through its endpoint, effect estimate, and uncertainty together. Overall survival is a time-to-event outcome, so the analysis must account for different follow-up durations and censoring. The medians offer an intuitive summary, while the hazard ratio summarizes the relative event experience across follow-up. Neither alone captures all of the information in the survival distribution.

The result also demonstrates the distinction between the direction of an estimate and the strength of evidence for a difference. The hazard ratio is below 1, but its confidence interval includes 1 and the reported p-value is above 0.05. A numerical direction is not sufficient to establish a treatment difference. At the same time, failure to establish a difference does not show equivalence. Precision and the range of effects compatible with the data are essential to interpretation.

The registry's description of stratification by visceral metastases and prior chemotherapy highlights how trial analyses may account for baseline prognostic factors. Yet the posted result gives limited detail about how the stated planned analysis relates to the reported analysis. That distinction matters when evaluating whether a result is adjusted, unadjusted, or aligned with the original plan.

The secondary outcomes show another important statistical issue: different endpoints can have different denominators, definitions, and inferential status. Without a reported multiplicity strategy, unadjusted secondary comparisons are better viewed as exploratory than as independent confirmation. Likewise, planning calculations based on an observed effect are not a substitute for the original trial design rationale or a measure of observed power.

Overall, this comparison is a useful example of reading a randomized trial result without turning a point estimate into a categorical claim. The evidence must be interpreted in the context of uncertainty, analysis choices, and gaps in the registry record.

20. 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 registry record gives a concise outcome description but does not include the full protocol or statistical analysis plan. It does not report the original sample-size justification, planned event target, interim analyses, or stopping rules. Consequently, planning illustrations based on the observed effect cannot establish what assumptions guided the original trial design.

For the primary outcome, the record states that a stratified log-rank test was planned and identifies the stratification factors. The posted analysis is labeled Log Rank, but its summary does not clarify whether it was stratified or provide a separate adjusted model result. The record also does not report diagnostics for the proportional hazards assumption, censoring details, or sensitivity analyses. Those omissions limit assessment of model fit and robustness.

The primary endpoint is described as intent to treat, but the registry summary does not explain the handling of missing outcome information, withdrawals, or treatment switching. The analysis counts for secondary outcomes differ from each other and from total enrollment; the record does not explain the reasons or provide detailed endpoint-specific population rules. Progression-free survival is listed as a secondary outcome, but its results are not reported in the registry record.

The safety summary provides counts and selected serious adverse event terms but does not report exposure-adjusted comparisons, timing, or a formal statistical analysis. The number of participants with an event is not necessarily the number of events, and the registry summary does not describe recurrent-event handling or attribution rules.

Finally, the registry's condition list covers several disease sites and stages, but the posted overall result does not provide subgroup estimates for those categories. The findings therefore should not be assumed to describe the effect in every listed subgroup separately.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Gemcitabine Hydrochloride and Cisplatin With or Without Bevacizumab in Treating Patients With Advanced Urinary Tract Cancer — NCT00942331.
• Registry record last updated 2026-06-24; status last verified 2026-05.
• Results first posted 2020-02-17.
• 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.

24. Record Summary

NCT00942331 is a completed randomized, double-blind, parallel-group phase III study sponsored by the National Cancer Institute. It enrolled 506 participants with advanced urinary tract cancer and compared gemcitabine and cisplatin with bevacizumab against gemcitabine and cisplatin with placebo.

The primary endpoint was overall survival in the intent-to-treat population. The posted median estimates were 14.5 months in Arm II and 14.3 months in Arm I. The reported hazard ratio was 0.87, with a 95% confidence interval from 0.72 to 1.06; the reported p-value was above 0.05. The primary comparison therefore does not establish a statistically significant difference in overall survival.

Objective response and grade 3 or higher toxicity are also posted as secondary outcomes, while a progression-free survival result is not reported in the registry record. The registry provides limited detail on multiplicity, missing-data handling, and the original design assumptions. Interpretation should retain the distinction between an uncertain comparison and evidence of equivalence.