Study of Sacituzumab Govitecan (SG) Versus Docetaxel in Participants With Advanced or Metastatic Non-Small Cell Lung Cancer (NSCLC): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Sacituzumab Govitecan (SG) Versus Docetaxel in Participants With Advanced or Metastatic Non-Small Cell Lung Cancer (NSCLC) (NCT05089734), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This is a randomized, parallel-group, open-label phase 3 study sponsored by Gilead Sciences. The registry record lists an enrollment of 603 and an estimated primary completion date of 2023-11-29. The study started on 2021-11-17 and its status is active, not recruiting. The registry record describes it as a global, multicenter study in participants with advanced or metastatic NSCLC whose disease progressed on or after platinum-based chemotherapy and anti-PD-1/PD-L1 immunotherapy.

Participants were assigned to SG or docetaxel. The posted primary analysis uses the ITT population and keeps participants in the group to which they were randomized. The arm counts reported for the primary outcome are 299 for SG and 304 for docetaxel. The study is open-label, so masking is listed as none; knowledge of assigned treatment could affect care or assessments that involve judgment. Overall survival is less dependent on subjective assessment than response or symptom outcomes, although the record does not describe procedures intended to manage potential open-label effects.

The treatment schedules differ. SG was given on Days 1 and 8 of each 21-day cycle, while docetaxel was given on Day 1 of each 21-day cycle. Both treatment descriptions specify continuation until progression, death, unacceptable toxicity, or another discontinuation criterion. The registry record does not report the original sample-size justification or the trial's original planning assumptions. It also does not report details of randomization procedures beyond randomized allocation, such as any stratification factors.

The primary endpoint is overall survival. Listed secondary outcomes include investigator-assessed progression-free survival, objective response rate, duration of response, and disease control rate under RECIST Version 1.1, along with adverse events, laboratory abnormalities, and symptom deterioration measured using the NSCLC-SAQ. Estimates are posted for overall survival, progression-free survival, objective response rate, and disease control rate. Results for the other listed outcomes 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: 784 participants were screened. Data submitted represent interim analysis performed on data collected by the Primary Completion Date. Complete data will be submitted in May 2026.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent to Treat (ITT) Analysis Set included all randomized participants according to the treatment arm to which the participant was randomized.

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 randomized participants according to the treatment arm to which the participant was randomized.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over Up to 24.4 months.

The primary endpoint, overall survival (OS), is the time from randomization until death from any cause. The registry record describes OS as estimated using the Kaplan-Meier method. Participants without documented death were censored on the date they were last known to be alive. Censoring means that a participant contributes follow-up information up to the last known time alive, even though the exact time of death is not observed in the record.

OS is used because it captures survival regardless of the specific cause of death and does not require a judgment that a tumor has progressed or responded. It is clinically direct, but its interpretation still depends on follow-up, completeness of death information, and the handling of censoring. The median is the estimated time by which half of the survival distribution has experienced the event; it is not the average survival time and does not describe the experience of every participant.

The registry reports median OS for each randomized arm, with 95% confidence intervals, and a sponsor-reported hazard ratio from a log-rank analysis. These statistics describe different aspects of the time-to-event data: the medians locate the midpoint of each estimated survival distribution, while the hazard ratio summarizes the relative event rate over follow-up under the analysis model. The registry gives the timeframe as up to 24.4 months. That timeframe is not a guarantee that every participant was followed for the same duration.

General statistical context: time-to-event methods can use information from participants who have not yet experienced the event by accounting for their observed follow-up through censoring. The resulting estimates rely on assumptions about censoring and the analysis; specific diagnostic checks or sensitivity analyses are not reported in the registry record.

7. Results Posted in the Registry

• Sacituzumab Govitecan (SG) vs Docetaxel: hazard ratio 0.84 (95% CI 0.68–1.04), reported p = 0.053 (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) Assessed by Investigator Per Response Evaluation Criteria in Solid Tumors (RECIST) Version 1.1

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Sacituzumab Govitecan (SG) vs Docetaxel: hazard ratio 0.92 (95% CI 0.77–1.11), reported p = 0.194 (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 (SG) vs Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate (ORR) Assessed by Investigator Per RECIST Version 1.1

• 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:
  • Docetaxel: 18.1% (55/304) versus 13.7% (41/299) on control; risk difference 4.4 percentage points (95% CI -1.4 to 10.2), risk ratio 1.32 (0.91–1.91); unadjusted two-proportion z-test p = 0.142.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

Disease Control Rate (DCR) Assessed by Investigator Per RECIST Version 1.1

• 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:
  • Docetaxel: 67.1% (204/304) versus 67.6% (202/299) on control; risk difference -0.5 percentage points (95% CI -7.9 to 7.0), risk ratio 0.99 (0.89–1.11); unadjusted two-proportion z-test p = 0.906.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span tumor response, disease control, progression, treatment-emergent adverse events, laboratory abnormalities, and reported symptoms. They do not all measure the same thing: some capture whether a tumor criterion was met, some capture the timing of progression, and others describe safety or patient-reported deterioration. Across the posted tumor outcomes, the comparative evidence is not uniformly decisive. That pattern does not overturn or independently confirm the primary OS result.

Secondary outcomes can help describe the trial's broader findings and the ways treatment groups may differ, but their interpretation depends on the endpoint definitions, assessment procedures, and statistical analysis. The registry lists duration of response, adverse-event outcomes, laboratory abnormalities, and NSCLC-SAQ symptom outcomes, but corresponding results for those listed measures are not reported in the registry record. Conclusions about those outcomes cannot be drawn from the listed outcome names alone.

Multiplicity matters because testing many outcomes increases the chance that at least one result may look unusual by chance, even when there is no underlying effect. General statistical context: a prespecified multiplicity strategy can control the overall false-positive risk, for example by adjusting the testing sequence or significance thresholds. The registry record does not report whether such a strategy was used. Accordingly, secondary p-values or comparisons should carry less weight than the primary analysis unless the full protocol and analysis plan establish how they were prioritized and controlled.

Secondary results are also not interchangeable with overall survival. Investigator-assessed response can be affected by the timing and judgment of assessments, while symptom outcomes rely on participant reports and safety outcomes depend on how events are collected and coded. Agreement across endpoints could add context, but disagreement is not automatically a contradiction because the measures reflect different clinical processes and time windows. The secondary findings are best viewed as supporting evidence requiring cautious interpretation, not as a collection of independent confirmatory tests.

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

• Progression-free Survival (PFS) Assessed by Investigator Per Response Evaluation Criteria in Solid Tumors (RECIST) Version 1.1
• Objective Response Rate (ORR) Assessed by Investigator Per RECIST Version 1.1
• Duration of Response (DOR) Assessed by Investigator Per RECIST Version 1.1
• Disease Control Rate (DCR) Assessed by Investigator Per RECIST Version 1.1
• Percentage of Participants Who Experienced Treatment Emergent Adverse Events (TEAEs)
• Percentage of Participants Who Experienced Grade 3 or 4 Treatment Emergent Laboratory Abnormalities Post-Baseline
• Time to First Deterioration in Shortness of Breath Domain as Measured by Non-small Cell Lung Cancer Symptom Assessment Questionnaire (NSCLC-SAQ)
• Time to First Deterioration in NSCLC-SAQ Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: randomization aims to make the assigned groups comparable at the start of a trial, on average, for measured and unmeasured factors. An ITT analysis retains participants in their randomized groups, regardless of later treatment changes, and preserves the comparison created by randomization. The registry defines the primary ITT population as all randomized participants analyzed according to the assigned arm. It does not report a separate treatment-received analysis for the primary endpoint.

How to read the time-to-event analysis

The registry reports OS medians estimated by Kaplan-Meier and a sponsor-reported hazard ratio analyzed using the log-rank method. Kaplan-Meier estimation incorporates the timing of events and censoring rather than treating every participant as if follow-up were complete. The median is read from the estimated survival distribution; its confidence interval reflects uncertainty around that estimate.

The hazard ratio compares event rates over follow-up in the two groups, as represented by the sponsor's analysis. A value below the null value for a ratio is in the direction of a lower event rate in the SG group, while a value above it is in the direction of a higher event rate. The reported confidence interval extends across the null value, so the data are compatible with no relative difference as well as with effects in either direction. The registry record does not report a test of the proportional-hazards assumption or a time-varying treatment-effect analysis. If hazards are not proportional, a single hazard ratio may not summarize the whole follow-up pattern well; this is a general consideration, not a reported finding about this trial.

The log-rank method compares the observed timing of events between groups across follow-up. Its p-value depends on the event information and the analysis assumptions. The record reports p=0.053 for the primary OS analysis. That value should be read alongside the estimated hazard ratio and its confidence interval, rather than as a stand-alone verdict. It does not quantify the probability that the treatment effect is exactly absent.

How to read the response outcomes

Objective response rate is the percentage meeting the response definition, assessed by the investigator using RECIST Version 1.1. Disease control rate is also investigator-assessed under RECIST Version 1.1. These binary outcomes classify participants by whether a criterion was met, unlike OS and progression-free survival, which incorporate event timing. The registry reports 95% confidence intervals around the arm-specific percentages. A confidence interval for an arm percentage expresses uncertainty in the underlying proportion given the observed data and statistical method.

The registry's sponsor-reported ORR analysis uses the Cochran-Mantel-Haenszel method and reports a difference in proportions. This method can form a comparison adjusted across strata, but the stratification details are not reported in the registry record. A crude, unadjusted calculation from summary data need not match a stratified analysis, particularly when the analysis weights groups differently. The posted unadjusted comparison is not a replacement for the sponsor's reported analysis. For DCR, the record posts arm-specific estimates but no sponsor-reported comparison.

Why confidence intervals matter

General statistical context: a confidence interval represents a range of estimates that are reasonably compatible with the observed data under a specified procedure. Wider intervals indicate less precision; narrower intervals indicate greater precision, all else being equal. An interval that includes a null value does not prove there is no effect. It indicates that the data do not exclude that null value at the interval's stated confidence level. The intervals also show the range of effect sizes that remain compatible with the analysis, which can be more informative than a threshold-based reading of a p-value.

Interpretation limits of the reported methods

The statistical methods are only partly described in the registry record. It identifies Kaplan-Meier estimation for OS, the log-rank method for the reported time-to-event comparisons, RECIST Version 1.1 for investigator-assessed tumor outcomes, and the Cochran-Mantel-Haenszel method for the sponsor-reported ORR comparison. The record does not report the full statistical analysis plan, any stratification factors, missing-data procedures for each endpoint, or whether any interim analyses were planned or conducted. These details should not be inferred from the posted estimates.

General statistical context: over-dispersion occurs when variation in the data is greater than a chosen model expects. It can make standard errors too small and confidence intervals too narrow if not handled appropriately. The registry outcomes do not report a model for over-dispersed data, and the record does not identify an over-dispersion issue. More broadly, the choice of model and any assumptions should be assessed using the analysis plan and supporting diagnostics, which are not reported in the registry record.

11. Confidence Intervals and Precision

The 95% confidence interval for median OS is 9.4 to 12.3 months for SG and 8.1 to 10.6 months for docetaxel. These intervals communicate uncertainty in each arm's estimated median. They overlap, but overlap between separate arm-specific intervals is not itself the formal test of the treatment comparison. The sponsor-reported hazard ratio and its confidence interval are the direct comparative summary posted for OS.

The OS hazard ratio confidence interval is 0.68 to 1.04. It includes the null value for a ratio, so the posted result does not exclude no relative difference. It also includes estimates on both sides of that null value, leaving uncertainty about direction and magnitude. The p-value of 0.053 is close to the conventional threshold sometimes used in trial analyses, but the registry does not report the trial's prespecified significance threshold or testing plan. The p-value should therefore not be treated as a stand-alone declaration.

For progression-free survival, the sponsor-reported hazard ratio confidence interval is 0.77 to 1.11, also spanning the ratio null value. The arm-specific intervals for response and disease control convey uncertainty in the proportions. In general, the width of an interval is affected by the amount of information, event frequency, and variability, as well as the statistical method. It is not a measure of clinical importance.

General statistical context: confidence intervals are not guarantees that the true value lies within the displayed range, and a 95% interval does not mean that 95% of participants experienced outcomes within that range. It describes a property of the interval-producing procedure under its assumptions. Interpretation is strongest when estimates, interval width, endpoint relevance, and trial design are considered together. The registry's timeframe is up to 24.4 months; estimates based on follow-up do not imply equal observation time for all participants.

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 are not the original trial design calculations. The stated 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. For time-to-event outcomes, the figures are total events, using the Schoenfeld method. For the other outcomes, figures are participants per arm.

The 80% power column gives the planned event total or per-arm participant count associated with an 80% chance of detecting the selected effect under those assumptions, if that effect were the true effect and the model assumptions held. The 90% power column describes the corresponding planning count for a higher chance of detection. These are design-planning concepts, not guarantees about what a future study would find.

For OS, planning for 100% of the observed effect gives total event illustrations of 1,033 for 80% power and 1,383 for 90% power. For 75% of the observed effect, the corresponding totals are 1,837 and 2,458; for 50%, they are 4,132 and 5,531. These figures are total events, not participants per arm. The progression-free survival planning figures are also total events: 4,516 and 6,046 for 100% of the observed effect, 8,028 and 10,748 for 75%, and 18,063 and 24,182 for 50%.

For ORR, the per-arm participant illustrations are 1,094 and 1,464 for 100% of the observed effect, 1,890 and 2,530 for 75%, and 4,129 and 5,526 for 50%. For DCR, the per-arm figures are 168,064 and 224,990 for 100%, 298,515 and 399,626 for 75%, and 671,055 and 898,352 for 50%. Smaller effects require more events or participants to detect under the stated assumptions. These are planning illustrations, not observed power.

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 = 0.840, so ln(HR) = -0.1744.
2. d = 4 × (1.96 + 0.842)² / [ln(0.840)]² = 1,032.8, rounded up to 1,033 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 <- 0.84                              # 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(5089734)
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 = 1,033 (80% power), 1,383 (90% power)
 75% of observed effect: events = 1,837 (80% power), 2,458 (90% power)
 50% of observed effect: events = 4,132 (80% power), 5,531 (90% power)
Simulated power with 1,033 events: 0.809 (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 1,668 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 603 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 <- 9.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.84          # 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: 1216         p (1-sided)   0.0001
  Events: 466        ~HR at bound   0.7091
    Month: 17    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.84   0.0338
    IA 2: 67%                   Z   2.5114
      N: 1668         p (1-sided)   0.0060
  Events: 932        ~HR at bound   0.8483
    Month: 28    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.84   0.5603
        Final                   Z   1.9930
      N: 1668         p (1-sided)   0.0231
 Events: 1398        ~HR at bound   0.8989
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.84   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 registry reports sponsor analyses for OS and progression-free survival using the log-rank method. The OS estimate is a hazard ratio of 0.84, with a 95% confidence interval of 0.68 to 1.04 and p=0.053. For progression-free survival, the hazard ratio is 0.92, with a 95% confidence interval of 0.77 to 1.11 and p=0.194. These are the reported comparative analyses for those time-to-event outcomes.

For ORR, the sponsor-reported analysis uses the Cochran-Mantel-Haenszel method and gives a difference in proportions of -4.3, with a 95% confidence interval of -10.1 to 1.5 and p=0.925. A simple unadjusted comparison based on posted summary values addresses a different analysis and may not reproduce a stratified sponsor analysis. The registry record does not report the strata or enough detail to reconstruct the sponsor's procedure. DCR has no sponsor-reported comparison in the registry record.

The record does not flag a discrepancy between reported and recalculated results. This does not make different methods interchangeable: when the sponsor's analysis and a simple unadjusted calculation target different comparisons or use different adjustment, their estimates and p-values can differ. Interpretation should identify which analysis is being discussed, and the sponsor's analysis should be kept distinct from an unadjusted recalculation.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies OS as the primary outcome and lists multiple secondary outcomes. It does not report whether the trial used a multiplicity adjustment, a hierarchical testing sequence, or another strategy to control the chance of false-positive findings across outcomes. It also does not report the prespecified significance threshold for the primary analysis or the complete statistical analysis plan. The planning illustration's two-sided significance level of 0.05 is an assumption for that illustration, not evidence of the trial's original testing rule.

The primary ITT analysis includes all randomized participants according to their randomized arm. For OS, participants without documentation of death were censored on the date they were last known to be alive. This describes the stated OS censoring rule, but does not by itself show how much follow-up was available or whether censoring was independent of the chance of death. The registry record does not report detailed missing-data procedures for the secondary outcomes, reasons for missing assessments, or sensitivity analyses addressing missingness.

For time-to-event endpoints, censoring is a standard way to retain partial follow-up when an event has not been documented. General statistical context: valid interpretation depends on assumptions about the relationship between censoring and the event process. If participants lost to follow-up differ systematically in their risk from those observed, estimates can be affected. The posted record does not report analyses that assess this possibility.

The primary analysis population is described, but populations used for each secondary analysis and rules for evaluable participants are not fully detailed in the registry record. It also does not report the handling of treatment discontinuation, subsequent therapies, or protocol deviations in the analysis. These omissions limit reconstruction of the complete analysis and prevent assessment of whether alternative analysis populations or missing-data methods would change the findings.

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 (8.3%), pneumonia (5.6%), diarrhoea (4.7%), neutropenia (3.5%), dyspnoea (2.4%).

The safety figures distinguish participants at risk from participants recorded with an event. For serious adverse events, the registry reports 137 among 296 at risk in the SG group and 124 among 288 at risk in the docetaxel group. For other adverse events, it reports 283 among 296 at risk for SG and 267 among 288 at risk for docetaxel. Death counts are reported as 168 for SG and 187 for docetaxel. These counts are descriptive and are not, by themselves, adjusted comparisons of treatment safety.

The serious adverse event terms listed include febrile neutropenia (8.3%), pneumonia (5.6%), diarrhoea (4.7%), neutropenia (3.5%), dyspnoea (2.4%), and general physical health deterioration (2.0%). The registry record does not specify in this summary whether these term percentages refer to the same denominator or provide a comparative statistical analysis for each term. They should not be interpreted as a complete account of all possible harms.

Safety comparisons require attention to exposure time, event definitions, severity, attribution, and whether participants could have more than one event. Those details are not fully reported in the registry record. The counts therefore describe the posted safety experience but do not establish that either treatment is safer overall.

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

The posted primary result estimates median OS at 11.1 months for SG and 9.8 months for docetaxel. The sponsor-reported hazard ratio is 0.84, with a 95% confidence interval of 0.68 to 1.04 and p=0.053. The estimate points toward a lower death hazard for SG in this analysis, but the interval includes the ratio null value and remains compatible with no relative difference. The result should be described with both its direction and its uncertainty.

These statistics do not show that every participant in one group lived longer than every participant in the other, nor do the medians predict an individual's survival. A median is a group-level summary of an estimated distribution. The hazard ratio summarizes relative event rates under the analysis and is not a direct translation into added months of life. The record does not report an absolute survival probability at a particular time point.

The trial is randomized, which supports a causal comparison of assigned treatment when the trial conduct and analysis assumptions are appropriate. However, the open-label design and unreported details of the analysis plan remain relevant when assessing the broader evidence. The posted results apply to the studied participants and follow-up described in the registry; they do not establish effects in populations or settings not represented by the trial.

Secondary findings address other outcomes and should not be substituted for the primary OS result. The record does not report results for several listed secondary measures, including duration of response and symptom deterioration. In addition, the absence of reported multiplicity procedures limits the strength of confirmatory claims based on multiple secondary comparisons.

General statistical context: a non-definitive estimate is not proof of no effect. It means that the available data and their precision do not settle the comparison. Conversely, an estimate favoring a group does not by itself prove a clinically important benefit. Clinical importance depends on the size and reliability of the effect, the outcome being measured, the balance of benefits and harms, and the circumstances of care. The registry results alone do not answer all of those questions.

19. Why This Trial Matters Statistically

This trial poses a randomized comparison of two active treatment regimens in advanced or metastatic NSCLC after progression on or after platinum-based chemotherapy and anti-PD-1/PD-L1 immunotherapy. That treatment context defines the clinical question; it should not be generalized automatically to other disease stages or treatment histories. The primary endpoint, OS, is an outcome that does not depend on investigator judgment of tumor response, while the secondary endpoints add information about progression, tumor response, safety, and symptoms.

Statistically, the important issue is not only which direction the point estimate favors, but how much uncertainty surrounds it. The OS hazard ratio estimate favors SG numerically, yet its confidence interval spans the ratio null value. That combination makes precision central to interpretation. The reported p-value should be read with the interval and endpoint definition rather than treated as a binary verdict.

The trial also illustrates why endpoint-specific methods matter. OS and progression-free survival are time-to-event outcomes; response and disease control are proportions; safety outcomes count events or affected participants. Different outcome types require different summaries and analyses, and a crude calculation for one endpoint does not stand in for a sponsor's adjusted analysis. Likewise, secondary comparisons should be interpreted in light of multiplicity and their role in the trial's testing plan.

Finally, the registry record provides useful information about the randomized design, endpoint definitions, reported estimates, and some analysis methods, but it does not include the full statistical analysis plan or several details needed to reconstruct all analyses. A statistically responsible reading distinguishes what the posted results estimate from what remains unknown, and avoids turning uncertain group-level findings into individual predictions.

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 trial is open-label, with masking listed as none. Knowledge of treatment assignment can influence care, reporting, and investigator assessment, particularly for endpoints that involve judgment. OS is less subject to assessment judgment than response or symptoms, but the registry record does not describe procedures for minimizing other potential effects of open-label treatment.

The registry provides a follow-up timeframe of up to 24.4 months, but it does not give the distribution of follow-up time across participants, the number of OS events at the analysis, or details of subsequent treatment. The OS censoring rule is stated, but no sensitivity analysis for censoring or missing outcome information is reported in the registry record. These omissions limit assessment of how robust the time-to-event estimates are to incomplete follow-up.

The complete protocol and statistical analysis plan are not reported in the registry record. In particular, it does not report the trial's original sample-size assumptions, planned significance threshold, multiplicity strategy, interim analysis plan, or details of randomization stratification. The sample-size illustrations based on observed effects are not substitutes for the original design rationale.

Several listed secondary outcomes do not have posted results in the registry record. For the outcomes with results, the record does not fully describe all analysis populations, missing-data rules, or assessment schedules. The sponsor-reported ORR analysis uses a method whose strata are not identified in the registry summary, limiting independent reconstruction. These limitations do not invalidate the reported estimates, but they restrict how completely the analyses can be evaluated from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Sacituzumab Govitecan (SG) Versus Docetaxel in Participants With Advanced or Metastatic Non-Small Cell Lung Cancer (NSCLC) — NCT05089734.
• Registry record last updated 2026-05-07; status last verified 2026-04.
• Results first posted 2025-01-14.
• 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

NCT05089734 is a randomized, open-label, parallel-group phase 3 study sponsored by Gilead Sciences. It compares sacituzumab govitecan-hziy with docetaxel in participants with advanced or metastatic NSCLC following progression on or after platinum-based chemotherapy and anti-PD-1/PD-L1 immunotherapy. The registry lists enrollment of 603, a start date of 2021-11-17, primary completion on 2023-11-29, and status active, not recruiting.

The primary endpoint is OS, analyzed in the ITT population. Median OS was 11.1 months for SG and 9.8 months for docetaxel; the sponsor-reported hazard ratio was 0.84, with a 95% confidence interval of 0.68 to 1.04 and p=0.053. The interval includes the ratio null value, so uncertainty remains about the comparative effect. Secondary outcome results provide additional context but do not replace the primary finding. The registry record does not report the complete analysis plan, multiplicity procedures, or results for several listed secondary outcomes.