Study of Sacituzumab Govitecan Versus Physician's Choice of Treatment in Participants With Urothelial Cancer That Cannot Be Removed or Has Spread: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Sacituzumab Govitecan Versus Physician's Choice of Treatment in Participants With Urothelial Cancer That Cannot Be Removed or Has Spread (NCT04527991), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

This question is clinically and statistically distinct from whether the groups differed in tumor response or time until disease progression. Overall survival captures death from any cause, while progression-free survival and response outcomes address other aspects of the disease course. The registry record lists progression-free survival, objective response rate, clinical benefit rate, and duration of response among the secondary outcomes.

3. Trial Design

This was a randomized, open-label, parallel-group phase III study. Participants were assigned to sacituzumab govitecan-hziy or treatment of physician’s choice. The registry record lists an enrollment of 711 and describes the study as completed. It records a start date of 2021-01-13 and a primary completion date of 2025-07-04.

In the sacituzumab govitecan-hziy group, treatment was administered intravenously on Day 1 and Day 8 of each 21-day cycle, at 10 mg/kg. In the physician’s-choice group, the investigator selected one of paclitaxel, docetaxel, or vinflunine before randomization. The registry record does not give a complete description of the comparator treatment schedule in the available arm description, so specific doses and schedules for those chemotherapy options are not reported in the registry record.

The study was open-label, meaning treatment assignment was not masked to participants or study personnel as described in the registry. This can matter for outcomes involving judgment or care decisions, although the primary outcome, death from any cause, is less dependent on subjective assessment than tumor response or progression. The record also lists progression-free survival assessed both by investigators and by blinded independent central review.

The primary analysis population was the intent-to-treat population, which included all randomized participants. The registry record reports 355.0 participants in the sacituzumab govitecan-hziy group and 356.0 in the physician’s-choice group for the primary outcome. The method used to generate the randomization sequence, allocation concealment procedures, stratification factors, and the original sample-size justification are 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.

Before assignment: 886 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in the Intent-to-treat (ITT) Analysis Set were analyzed. The ITT Analysis Set included all participants who have been randomized to the trial.

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.

Population: The Intent-to-treat (ITT) Analysis Set included all participants who have been randomized to the trial.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over Up to 42 months.

Overall survival was the primary endpoint. It was defined as the time from randomization to death from any cause, and the registry record states that it was analyzed with Kaplan-Meier estimates. The reported timeframe is up to 42 months.

Overall survival is a time-to-event outcome: the analysis accounts for the timing of deaths and for participants whose survival time is not yet fully observed at the analysis cutoff. The median survival is the point at which the estimated survival curve reaches one-half. It describes the middle of the estimated survival-time distribution; it does not describe every participant’s survival time or the length of benefit for an individual.

The endpoint is used because it captures death regardless of its cause and does not require a judgment about whether a tumor has progressed. The registry record also reports a hazard ratio comparing the randomized groups. A hazard ratio summarizes the relative event rate over follow-up under the analysis model; it is not a difference between the two median survival times. The median estimates and hazard ratio therefore answer related but non-identical questions.

Kaplan-Meier estimation and the hazard-ratio analysis rely on follow-up and censoring information. The registry record identifies the analysis method but does not report detailed censoring rules or other implementation details. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Sacituzumab Govitecan-hziy (SG) vs Treatment of Physician's Choice: hazard ratio 0.86 (95% CI 0.73–1.02), reported p = 0.087 (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.

Progression-Free Survival (PFS) by Investigator Assessment

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Stratified Log-rank); it was not recalculated.
• Result:
  • Sacituzumab Govitecan-hziy (SG) vs Treatment of Physician's Choice: hazard ratio 0.81 (95% CI 0.68–0.95), reported p = 0.012 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Sacituzumab Govitecan-hziy (SG) vs Treatment of Physician's Choice than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Progression-Free Survival (PFS) by Blinded Independent Central Review (BICR)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Stratified Log-rank); it was not recalculated.
• Result:
  • Sacituzumab Govitecan-hziy (SG) vs Treatment of Physician's Choice: hazard ratio 0.86 (95% CI 0.72–1.03), reported p = 0.110 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Sacituzumab Govitecan-hziy (SG) vs Treatment of Physician's Choice and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate (ORR) by Investigator Assessment

• 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:
  • Treatment of Physician's Choice: 15.7% (56/356) versus 19.7% (70/355) on control; risk difference -4.0 percentage points (95% CI -9.6 to 1.6), risk ratio 0.80 (0.58–1.10); unadjusted two-proportion z-test p = 0.164.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment of Physician's Choice and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the picture beyond overall survival. They include progression-free survival assessed by investigators and by blinded independent central review, as well as response, clinical benefit, and duration-of-response measures. The record therefore includes both time-to-event outcomes and outcomes based on tumor assessment.

Across the posted secondary results, the pattern is not uniformly conclusive across outcomes and assessment approaches. The investigator-assessed progression-free survival comparison has a reported hazard-ratio interval that excludes 1, while the central-review progression-free survival interval includes 1. The response comparison also has uncertainty that includes no difference on the sponsor-reported odds-ratio scale. These results should be read as outcome-specific estimates, not as interchangeable confirmations of the primary endpoint.

Progression-free survival and tumor response are related to disease control, but they do not measure death from any cause in the same way as overall survival. Differences in endpoint definitions, assessment processes, and follow-up can contribute to variation across outcomes. The central-review assessment offers a different assessment approach from investigator review, but the registry record does not provide enough detail to attribute the difference between estimates to any particular cause.

Secondary findings generally carry less inferential weight when many outcomes are examined and the record does not report a multiplicity adjustment or a prespecified testing hierarchy. Repeated testing can increase the chance that at least one result appears statistically persuasive by chance alone. The registry record does not report how multiplicity across the secondary outcomes was controlled. Consequently, these outcomes are useful context but should not be treated as independent proof of the primary question or as a substitute for the primary overall-survival analysis.

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

• Progression-Free Survival (PFS) by Investigator Assessment
• Progression-Free Survival (PFS) by Blinded Independent Central Review (BICR)
• Objective Response Rate (ORR) by Investigator Assessment
• Objective Response Rate (ORR) by BICR
• Clinical Benefit Rate (CBR) by Investigator Assessment
• Clinical Benefit Rate (CBR) by BICR
• Duration of Objective Tumor Response (DOR) by Investigator Assessment
• Duration of Objective Tumor Response (DOR) by BICR

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports Kaplan-Meier estimates for overall survival and a stratified hazard ratio from a log-rank analysis. These methods are designed for time-to-event data, where the event is death and some participants may not have an observed event by the end of the analysis period.

What does a Kaplan-Meier estimate represent?

In general, Kaplan-Meier estimation builds a survival curve from the observed event times while retaining information from participants who are followed for a period but do not have an observed event before their follow-up ends. Such participants are censored at the end of their known follow-up rather than treated as if they had died. The curve estimates the proportion surviving over time, subject to assumptions about censoring and follow-up. Its median is the time at which the estimated survival probability reaches one-half, when that point is estimable.

The registry record defines overall survival as time from randomization to death from any cause and says Kaplan-Meier estimates were used. Detailed rules for censoring, data cutoff, and handling of incomplete follow-up are not reported in the registry record. These details can affect the construction and interpretation of a survival curve.

How should the hazard ratio be understood?

In general, a hazard is the instantaneous event rate among people who have not yet experienced the event, conditional on having remained event-free up to that time. A hazard ratio compares those rates between groups over follow-up under the analysis. A value below 1 is oriented toward a lower event hazard in the first-named group, while a value above 1 is oriented toward a higher event hazard. This is a relative summary, not an absolute difference in survival time and not a statement about the outcome for every participant.

The registry reports a stratified hazard ratio and a log-rank method for overall survival. Stratification generally accounts for specified grouping factors in the comparison, but the factors used are not reported in the registry record. The hazard-ratio interpretation also depends on the analysis assumptions and the way the treatment contrast is summarized over time. The record does not report a detailed assessment of those assumptions.

What does a confidence interval add?

In general, a confidence interval expresses statistical uncertainty around an estimate under the method used. A wider interval indicates less precision than a narrower interval on the same scale. For a hazard ratio, 1 represents equal hazards under the ratio scale. An interval that contains 1 includes the no-relative-difference value among the estimates compatible with the analysis at that confidence level. An interval that excludes 1 does not by itself establish clinical importance, nor does it remove the need to consider analysis choices and other evidence.

The primary hazard-ratio interval extends from 0.73 to 1.02. Its upper endpoint is close to 1, and the interval includes 1. The reported p value is 0.087. The registry’s reported analysis is the principal basis for describing this comparison; a median contrast should not be substituted for it.

Why is the log-rank method used?

In general, a log-rank test compares the observed distribution of event times between groups across follow-up, taking account of the number of participants at risk over time. It is often used with survival data because it uses timing information rather than reducing each participant’s experience to an event/no-event status at a single cutoff. The registry identifies log-rank analysis for the primary result and stratified log-rank analysis for the listed progression-free survival comparisons.

The registry record does not provide the full statistical analysis plan, the prespecified significance threshold for the primary comparison, the exact stratification factors, or any planned interim-analysis procedures. Those aspects are not reported in the registry record and should not be inferred from the posted endpoint results alone.

For the binary response outcome, the sponsor’s reported method is Cochran-Mantel-Haenszel with a stratified odds ratio. In general, an odds ratio compares the odds of an outcome between groups, and a stratified version combines information across specified strata. It is not the same as a risk difference or risk ratio. The registry record does not identify the strata used in that response analysis.

11. Confidence Intervals and Precision

The primary median estimates have 95% confidence intervals of 9.1 to 11.8 months for sacituzumab govitecan-hziy and 7.5 to 9.7 months for physician’s choice. These intervals express uncertainty in each group’s median estimate. They are not intervals for the between-group treatment effect, and overlap or non-overlap of separate group intervals is not a substitute for the reported comparative analysis.

The comparative estimate is the stratified hazard ratio of 0.86, with a 95% confidence interval from 0.73 to 1.02. Its interval spans the no-difference value of 1. This means the estimate is not highly precise enough to rule out that value at the stated confidence level. The range also permits effects in either direction around 1, although most of its range lies below 1. The reported p value, 0.087, is consistent with uncertainty in the primary comparison rather than a definitive separation under a conventional significance interpretation.

In general, a 95% confidence interval is generated by a procedure that, under its assumptions, would cover the underlying parameter in 95% of repeated comparable studies. It is not a statement that there is a 95% probability that the fixed parameter lies within this particular interval. The interval’s practical meaning also depends on the endpoint, population, analysis method, and follow-up.

The median intervals and hazard-ratio interval quantify different quantities, so their widths cannot be compared directly. Precision is also distinct from clinical importance: a statistically precise estimate might still be small in practical terms, while an imprecise estimate may include effects that matter in either direction. The registry record does not report a prespecified threshold for a clinically important overall-survival effect, so such a threshold cannot be assessed from this record.

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 illustrations based on the observed effects, not the original trial design calculations. For time-to-event outcomes, the listed values are total events needed, not participants per arm. For other outcome types, the values are participants per arm. The figures use the stated effect fractions: planning for 100%, 75%, or 50% of the observed effect.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The time-to-event illustrations use the Schoenfeld approach. The original design assumptions and sample-size justification are not reported in the registry record.

In plain language, a target of 80% power means that, if the assumed effect were the true effect and the other planning assumptions held, the design would have an 80% chance of detecting that effect at the stated significance level. The 90% power column applies the same idea with a higher chance of detection, which generally requires more events or participants. These are planning concepts, not a guarantee that a study will detect an effect.

Smaller assumed effects require more information to distinguish them from no effect at the same power and significance level. Thus, planning for 75% or 50% of the observed effect produces larger requirements than planning for the full observed effect. These figures are not observed power. They are illustrative calculations from the observed estimate, and they do not establish the power of the completed trial or the design choices made for it.

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 = 0.860, so ln(HR) = -0.1508.
2. d = 4 × (1.96 + 0.842)² / [ln(0.860)]² = 1,380.2, rounded up to 1,381 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 <- 0.86                              # 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(4527991)
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 = 1,381 (80% power), 1,848 (90% power)
 75% of observed effect: events = 2,454 (80% power), 3,285 (90% power)
 50% of observed effect: events = 5,521 (80% power), 7,391 (90% power)
Simulated power with 1,381 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 2,183 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 711 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 <- 9          # control-arm median, months (converted from the posted unit)
hr          <- 0.86          # 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: 1548         p (1-sided)   0.0001
  Events: 623        ~HR at bound   0.7428
    Month: 17    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.86   0.0338
    IA 2: 67%                   Z   2.5114
      N: 2184         p (1-sided)   0.0060
 Events: 1246        ~HR at bound   0.8673
    Month: 27    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.86   0.5603
        Final                   Z   1.9930
      N: 2184         p (1-sided)   0.0231
 Events: 1869        ~HR at bound   0.9119
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.86   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 primary comparison reported by the registry is the sponsor’s own stratified hazard-ratio analysis using a log-rank method: 0.86, with a 95% confidence interval from 0.73 to 1.02 and p = 0.087. The posted analysis is therefore the basis for interpreting the primary result. The calculation described as a recalculation is not a replacement for that analysis; it is an unadjusted calculation from posted summary statistics and may not reproduce the sponsor’s stratification or other analysis details.

For this primary endpoint, the record does not flag a discrepancy between the posted result and the recalculation. Even so, the sponsor’s analysis remains the relevant reported inferential result because it is the analysis recorded for the trial. The reported interval includes 1, so the result does not give a precise separation from the no-relative-difference value under this analysis.

In general, differences between a reported analysis and a simple recalculation can arise because the reported method uses participant-level data, stratification, censoring information, or other details that cannot be reconstructed from summary values alone. No such discrepancy is flagged for the primary comparison in this record, and undocumented details should not be presumed.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies overall survival as the primary endpoint and lists numerous secondary outcomes, including progression-free survival, response, clinical benefit, and duration of response, with some measures assessed in more than one way. When several outcomes are tested, the chance of at least one apparently positive result can rise if each is interpreted separately without adjustment. A prespecified testing hierarchy or multiplicity procedure can address this concern, but the planned approach is not reported in the registry record.

The posted secondary analyses include p values and confidence intervals for selected outcomes. The registry record does not state whether those analyses were adjusted for multiplicity, whether testing was hierarchical, or which secondary comparisons were confirmatory rather than exploratory. Their inferential strength should therefore be considered in light of that missing information. The absence of a reported adjustment does not prove that none was used; it means the approach is not reported in the registry record.

The primary population is defined as the intent-to-treat analysis set, comprising all participants randomized to the trial. This population preserves the randomized comparison as specified in the record. The registry record does not give a detailed account of exclusions, missing endpoint data, censoring rules, or sensitivity analyses for missing data. Those details are not reported in the registry record.

In general, missing outcome information can affect an estimate if the people with incomplete follow-up differ systematically from those whose outcomes are observed. For time-to-event analyses, censoring methods use the known follow-up while relying on assumptions about the relationship between censoring and future event risk. The record does not describe diagnostic checks or alternative assumptions. It is therefore not possible to assess from the registry entry alone how sensitive the results are to all missing-data or censoring choices.

Interim monitoring, stopping rules, and the full statistical analysis plan are also not reported in the registry record. No conclusion about those procedures should be inferred from the final posted comparisons.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (10.6%), diarrhoea (8.6%), neutropenia (4.6%), urinary tract infection (4.6%), sepsis (3.4%).

The registry lists serious adverse events affecting 185 participants in the sacituzumab govitecan-hziy group, among 349 at risk, and 110 participants in the physician’s-choice group, among 337 at risk. These are counts of participants affected, not counts of individual event episodes. They describe the posted serious-adverse-event summary and should be read alongside the group-specific numbers at risk.

The listed serious adverse-event terms include febrile neutropenia at 10.6%, diarrhoea at 8.6%, neutropenia at 4.6%, urinary tract infection at 4.6%, sepsis at 3.4%, and pyrexia at 3.2%. The registry record also lists participants affected by other adverse events and deaths, but the figures do not by themselves establish that an event was caused by study treatment. No causal attribution should be inferred from these counts alone.

In general, safety comparisons depend on how events were defined, collected, graded, and followed, as well as the time participants were exposed to treatment. Detailed exposure-adjusted analyses and the full adverse-event definitions are not reported in the registry record. The raw group summaries are descriptive; they should not be read as a complete assessment of comparative safety or as an individual risk estimate.

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

The posted primary analysis estimates median overall survival of 10.3 months for sacituzumab govitecan-hziy and 9.0 months for physician’s choice. The comparative hazard ratio is 0.86, with a 95% confidence interval from 0.73 to 1.02. Because the interval includes 1, the primary result remains compatible with no relative difference in the hazard as well as with a range of effects around that value. The analysis does not establish a definitive overall-survival difference.

This finding does not show that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to test whether differences fall within that margin; such a margin is not reported in the registry record. Nor does an uncertain result prove that there is no effect. It indicates that the posted primary estimate is not precise enough to rule out the no-difference value at the reported confidence level.

The group medians do not predict how long any individual will live, and the hazard ratio does not mean that each participant’s risk changed by a fixed amount. Both are population-level summaries from the trial’s analysis. The results apply to the study population and should not be generalized beyond what the record supports.

The secondary results address progression and tumor response rather than overall survival and have their own uncertainty and analysis considerations. They can provide context, but they do not overturn or replace the primary endpoint. The record does not report a multiplicity strategy for those secondary tests, which limits how strongly they can be treated as confirmatory.

The posted safety counts are descriptive and do not establish causation. The registry record also lacks detailed reporting on missing-data procedures, follow-up implementation, and subgroup effects. Those limits mean the results should be interpreted as the reported trial estimates, not as a complete account of every benefit, harm, or outcome for every participant.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical-trial result should be read through its endpoint, estimate, and uncertainty together. The median overall-survival estimates describe the survival curves at a particular point, while the hazard ratio summarizes the randomized comparison over follow-up. Neither statistic alone captures every feature of the observed data.

The primary confidence interval is especially important: it includes the no-relative-difference value even though the point estimate is below 1. That distinction prevents a point estimate from being mistaken for a conclusive treatment effect. The reported p value is also part of the inferential result, but it does not measure the probability that the treatment has no effect or the probability that the result is due to chance.

The record also provides outcomes based on progression and response, with more than one assessment approach. This creates a useful example of how outcomes can address related but distinct questions, and why agreement across analyses cannot be assumed. Interpretation of multiple endpoints requires attention to prespecification and multiplicity; those details are not reported in the registry record.

Finally, planning illustrations derived from observed effects should not be confused with the trial’s original design or with the completed study’s power. The registry entry does not report the original sample-size justification or design assumptions. Keeping design planning, observed estimates, and inferential uncertainty separate is essential to a statistically careful reading of a completed trial.

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 has limits that are specific to interpreting this trial. Although it identifies the study as randomized, open-label, and parallel-group, it does not report the sequence-generation method, allocation concealment procedures, or the factors used for stratification. Those omissions restrict assessment of design and analysis details from the registry entry alone.

The primary endpoint and Kaplan-Meier method are described, but detailed censoring rules, the data cutoff, and sensitivity analyses are not reported in the registry record. The entry does not provide a full statistical analysis plan or specify interim analyses and stopping rules. These details could clarify how the posted estimates were generated and how robust they are to alternative assumptions.

The record lists multiple secondary endpoints and assessment approaches, but does not report a multiplicity strategy or a testing hierarchy. That makes it difficult to determine which secondary findings were intended as confirmatory. The available arm description for physician’s choice is incomplete, so the exact treatment schedules and exposure details for its chemotherapy options are not reported in the registry record.

The safety summary gives counts and selected event terms, but the registry record does not provide the full context needed to compare event timing, duration, severity grading, treatment exposure, or causal attribution. Subgroup estimates and detailed missing-data procedures are also not reported in the registry record. These limits do not invalidate the posted results; they define what can and cannot be concluded from this registry summary.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Sacituzumab Govitecan Versus Physician's Choice of Treatment in Participants With Urothelial Cancer That Cannot Be Removed or Has Spread — NCT04527991.
• Registry record last updated 2026-06-02; status last verified 2026-05.
• Results first posted 2026-06-02.
• 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

The registry record describes a completed randomized, open-label phase III comparison of sacituzumab govitecan-hziy with treatment of physician’s choice in participants with locally advanced unresectable or metastatic urothelial cancer. The primary endpoint was overall survival in the intent-to-treat population, analyzed using Kaplan-Meier estimates.

The reported median overall survival was 10.3 months for sacituzumab govitecan-hziy and 9.0 months for physician’s choice. The stratified hazard ratio was 0.86, with a 95% confidence interval from 0.73 to 1.02 and reported p value 0.087. The interval includes 1, so the posted primary analysis does not establish a clear relative difference.

Secondary outcomes include progression-free survival and tumor-response measures, and the record reports serious adverse-event summaries. Important details—including multiplicity handling, full missing-data procedures, stratification factors, and the original sample-size justification—are not reported in the registry record.