HERTHENA-Lung01: Patritumab Deruxtecan in Subjects With Metastatic or Locally Advanced EGFR-mutated Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for HERTHENA-Lung01: Patritumab Deruxtecan in Subjects With Metastatic or Locally Advanced EGFR-mutated Non-Small Cell Lung Cancer (NCT04619004), a randomized phase 2 study. The primary outcome is Objective Response Rate (ORR) as Assessed by Blinded Independent Central Review (BICR).

2. Clinical Question

3. Trial Design

HERTHENA-Lung01 (NCT04619004) is a randomized, open-label, parallel-group Phase 2 study sponsored by Daiichi Sankyo. The registry lists enrollment of 277 and gives a study start date of 2021-02-02 and a primary completion date of 2022-11-21. The record status is active, not recruiting. It describes a population with metastatic or locally advanced NSCLC with an activating EGFR mutation who had received and progressed on or after at least 1 EGFR TKI and 1 platinum-based chemotherapy-containing regimen.

The two randomized groups received patritumab deruxtecan: one at a fixed dose of 5.6 mg/kg intravenously every 3 weeks, and the other by an up-titration regimen intravenously every 3 weeks. The registry does not give the up-titration dose steps in the arm description. As both groups receive the same named drug, the comparison concerns the regimens described in the record, rather than patritumab deruxtecan versus no treatment or versus another drug.

The primary outcome is objective response rate assessed by blinded independent central review. This creates a distinction between the open-label treatment assignment and the primary endpoint review: the study itself had no masking, but BICR is the stated assessor for the primary response outcome. The registry defines response using confirmed complete or partial response under RECIST v1.1 and identifies the Efficacy Analysis Set as the assessed population.

Registry enrollment and the denominators used for the primary outcome are different recorded quantities: enrollment is 277, while the outcome arm counts list 225 and 50. The registry record does not explain this distinction further. The protocol’s allocation procedure, detailed conduct of the up-titration regimen, and 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Objective response rate was assessed in the Efficacy Analysis Set.

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: Demographic and baseline characteristics were reported from the Full Analysis Set.

6. Primary Endpoint

The registry lists the primary outcome as Objective Response Rate (ORR) as Assessed by Blinded Independent Central Review (BICR), measured over Data collected from screening until time of disease progression by BICR, death, lost to follow up, study discontinuation, whichever occurs first, assessed up to approximately 21 months.

The primary endpoint is objective response rate as assessed by blinded independent central review. It is defined as the proportion of participants whose best overall response was a confirmed complete response or confirmed partial response, assessed by BICR according to RECIST v1.1. A complete response means disappearance of all target lesions; a partial response means at least a 30% decrease in the sum of diameters of target lesions.

Response rate is a binary endpoint at the participant level: each participant is classified according to whether a qualifying response was recorded. The measure therefore gives a direct account of how many participants in the assessed population met the response definition. It does not, by itself, describe how long a response lasted, how quickly it began, or what happened to participants who did not meet the response definition. The registry lists duration of response, time to tumor response, progression-free survival, and overall survival as separate secondary outcomes.

Central review is relevant because the trial was open-label, while the endpoint definition relies on imaging assessment. BICR provides the stated primary assessment independently of the investigator assessment. The registry does not report the detailed review procedures or whether any adjudication was needed. The response endpoint is assessed from screening until a listed stopping event, up to approximately 21 months.

7. Results Posted in the Registry

• Patritumab Deruxtecan Up-Titration: 16.0% (8/50) versus 28.4% (64/225) on control; risk difference -12.4 percentage points (95% CI -24.2 to -0.7), risk ratio 0.56 (0.29–1.10); unadjusted two-proportion z-test p = 0.070.

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 Rate (ORR) as Assessed by the Investigator

• 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:
  • Patritumab Deruxtecan Up-Titration: 16.0% (8/50) versus 24.9% (56/225) on control; risk difference -8.9 percentage points (95% CI -20.5 to 2.7), risk ratio 0.64 (0.33–1.26); unadjusted two-proportion z-test p = 0.178.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patritumab Deruxtecan Up-Titration and the control. The interval gives the range of effects that remain compatible with the data.

The registry names a broad set of secondary outcome domains: response assessed by investigators, duration of response, progression-free survival, disease control, time to tumor response, best percentage change in tumor diameters, overall survival, and treatment-emergent, serious, and special-interest adverse events. These outcomes extend the primary response question by covering response from other perspectives, disease course, survival, and safety. They are not interchangeable measures: for example, a response proportion does not describe response duration or time to progression.

The posted numerical secondary efficacy comparison is investigator-assessed ORR. Its unadjusted contrast points in the same direction as the primary BICR comparison, but it is a separate assessment and remains secondary. The other named secondary domains do not have reported analyses in the registry record. Thus, the outcome list indicates what the study intended to assess, but does not itself provide evidence about those outcomes.

Unadjusted secondary findings generally carry less inferential weight than a prespecified primary result when many outcomes are examined. Without a reported multiplicity strategy, it is unclear whether and how the study accounted for the number of endpoints or comparisons when interpreting statistical evidence. The record also does not report an analysis hierarchy linking the primary and secondary outcomes. Therefore, the secondary findings should be treated as supplementary descriptions rather than a set of independent confirmations of the primary result.

The registry identifies 8 secondary outcomes and lists no reported analyses for them. The absence of posted analyses does not establish that analyses were never conducted; it means their results and methods are not reported in the registry record. No broader pattern across duration, survival, tumor change, or safety efficacy outcomes can be inferred from the endpoint names alone.

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

• Duration of Response (DoR)
• Progression-free Survival (PFS)
• Objective Response Rate (ORR) as Assessed by the Investigator
• Disease Control Rate (DCR)
• Time to Tumor Response (TTR)
• Best Percentage Change in the Sum of Diameters (SoD) of Measurable Tumors
• Overall Survival (OS)
• Incidence of Treatment Emergent Adverse Events (TEAEs), Serious Adverse Events (SAEs), and Adverse Events of Special Interest (AESIs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level measure: a participant either met the confirmed response definition or did not. The posted arm results are counts, and the comparison expresses the difference in response proportions between the up-titration regimen and the 5.6 mg/kg regimen. The registry record names the assessed population as the Efficacy Analysis Set, but does not provide its full inclusion rules or explain how missing or unevaluable assessments were handled.

What does a risk difference describe?

A risk difference subtracts one group’s event proportion from the other group’s event proportion. Here, the event is a confirmed complete or partial response under the stated BICR and RECIST v1.1 definition. The sign depends on the order of subtraction: the posted comparison is up-titration relative to the 5.6 mg/kg group. A negative value therefore corresponds to a lower observed response proportion in the up-titration group. The difference is on the proportion scale, so it represents an absolute contrast rather than a relative ratio.

The registry also presents risk-ratio and odds-ratio summaries for the primary comparison. These use different scales. A risk ratio compares event proportions by division, while an odds ratio compares the odds of the event. Their numerical values should not be read as though they were risk differences. Such measures can offer complementary descriptions, but none removes the uncertainty arising from the observed group sizes or from limitations in the analysis record.

How should the confidence interval be understood?

A confidence interval communicates the uncertainty around an estimated effect under the assumptions of the procedure used to calculate it. For this risk difference, the interval extends from -0.242 to -0.007. It indicates that the estimate is not infinitely precise: a range of values remains compatible with the data and the calculation method. A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it describe the range of outcomes for individual participants.

The registry record does not state the method used to form the posted confidence interval. The unadjusted comparisons are recalculations from posted summary statistics, rather than a substitute for a sponsor’s complete analysis. The registry does not list a sponsor-reported comparative analysis for these outcomes. Accordingly, the recalculated comparison should be read as a transparent summary of the recorded counts, not as evidence that a particular regression model or covariate adjustment was used.

What does an unadjusted p-value convey?

An unadjusted p-value describes how unusual the data, or a result more extreme, would be under a specified null hypothesis and the calculation’s assumptions. The primary comparison has p = 0.07. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry labels this value unadjusted. The record does not report whether the study used a different prespecified test, covariate-adjusted model, or analysis hierarchy for the sponsor’s primary inference.

“Unadjusted” also matters when several outcomes or comparisons are considered. If many tests are examined, the chance of seeing a seemingly notable result can increase unless the analysis plan controls for multiplicity. The registry lists multiple secondary outcomes but does not state a multiplicity procedure. That absence does not show that no such plan existed; it means that the plan is not reported in the registry record.

What is not established by the posted methods?

The registry identifies randomization, an open-label design, parallel groups, the primary endpoint, and the response criteria. It does not report the method of sequence generation, allocation concealment, stratification factors, planned handling of intercurrent events, or details of missing-data sensitivity analyses. The original sample-size calculation and the trial’s own design assumptions are not reported in the registry record. The posted sample-size illustrations are separate planning calculations based on observed effects and should not be mistaken for those original design choices.

For a response outcome, incomplete assessments can affect which participants contribute to the numerator or denominator. Whether participants with missing or unevaluable scans were counted as nonresponders, excluded, or handled another way is not reported in the registry record. The registry states that the primary population was the Efficacy Analysis Set, but that label alone does not resolve these implementation details. These uncertainties are relevant to interpreting the precision and generalizability of the observed proportions.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.124, with a 95% confidence interval from -0.242 to -0.007. The interval gives more context than the point estimate alone: it shows that the comparison is uncertain and that the plausible values under the calculation span a meaningful range. The upper endpoint is close to zero, while the lower endpoint is further into the negative direction. The posted unadjusted p-value is 0.07. The registry record does not report the method used for the confidence interval or the test.

Precision differs between the groups because the outcome denominators differ: the 5.6 mg/kg group has 225 participants in the primary results, whereas the up-titration group has 50. A smaller denominator generally yields less precise estimates, all else being equal. This is a general statistical point, not an additional trial result. The broad interval around the difference is consistent with uncertainty in the comparison; it should not be replaced by a single definitive interpretation based only on the point estimate.

The risk-ratio interval is 0.288 to 1.097, and the odds-ratio interval is 0.213 to 1.077. These are alternative effect scales, not additional independent studies. The registry’s unadjusted risk-difference interval does not include zero, while the displayed ratio intervals include 1. Because the calculation methods are not reported, and because these summaries are derived from the same posted outcome data, apparent differences in their interval boundaries should be interpreted cautiously rather than treated as separate evidence.

For the investigator-assessed secondary ORR, the risk-difference interval is -0.205 to 0.027. That interval includes zero. It represents a different assessment of response and is secondary, so it does not replace the primary BICR result. The registry provides no reported analysis details sufficient to determine whether the two endpoint assessments were formally compared or incorporated into a hierarchy.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. The registry’s stated illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated participants per arm for a design that would have an 80% chance of detecting the assumed effect if that effect were the true one and the planning assumptions held. The 90% power column gives the corresponding per-arm planning figure for a higher chance of detection under those assumptions. These are design-planning concepts, not measures of how likely the trial result is to be true.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The table shows that smaller target effects require more participants per arm to achieve the stated power levels under the same planning framework. For the primary endpoint, the displayed per-arm figures increase from 175 and 233 when planning for 100% of the observed effect, to 766 and 1,025 when planning for 50% of the observed effect. These are illustrations derived from the observed comparison, not the trial’s original design rationale.

This is not observed power. It is a planning illustration and does not assess whether the completed study had sufficient power after seeing its result. The displayed figures do not establish that the study was designed around the observed effect, and they do not substitute for the protocol’s original sample-size calculation, which is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.284; treatment proportion p₁ = 0.160; average p̄ = 0.222.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5879 = 1.1524.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5813 = 0.4893.
4. n = (1.1524 + 0.4893)² / (-0.1244)² = 174.0, rounded up to 175 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.284444444444444                          # control proportion
p1 <- 0.16                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4619004)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 175 (80% power), 233 (90% power)
 75% of observed effect: n per arm = 326 (80% power), 436 (90% power)
 50% of observed effect: n per arm = 766 (80% power), 1,025 (90% power)
power.prop.test: 174 
Simulated power at n = 175 per arm: 0.810 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and multiple secondary outcomes, but does not report a multiplicity adjustment or a hierarchical testing strategy. When a study examines several outcomes, unadjusted tests can produce apparently notable results by chance even if none of the underlying effects is present. A prespecified strategy can control how evidence is interpreted across outcomes. Without a reported strategy, the unadjusted p-values should not be read as if they were necessarily adjusted for all planned analyses.

The primary comparison is reported with an unadjusted p-value. The investigator-assessed ORR comparison is also unadjusted. The record does not state whether these were part of a formal testing sequence, whether secondary endpoints were intended to support confirmatory claims, or how any additional comparisons were handled. The absence of that information does not prove that multiplicity was ignored; the strategy is simply not reported in the registry record.

Missing-data handling is also not described in sufficient detail. The primary endpoint timeframe includes assessment until progression, death, loss to follow-up, study discontinuation, or the stated maximum assessment period. The registry does not explain how missing scans, incomplete follow-up, or unevaluable response assessments contributed to the response denominator. It also does not report sensitivity analyses evaluating alternative assumptions for missing outcomes.

The primary population is identified as the Efficacy Analysis Set, but its full definition and relationship to all randomized participants are not reported. The record does not describe whether analyses used an intention-to-treat population, how protocol deviations were addressed, or which participants were excluded from efficacy analyses. Nor does it report details of censoring rules for the time-to-event secondary outcomes. These gaps constrain assessment of whether the posted outcome counts represent all randomized participants or a selected analysis population, and how robust any result might be to alternative analytical choices.

15. 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: disease progression (8.0%), pneumonitis (4.0%), pleural effusion (4.0%), anaemia (2.7%), pneumonia (2.2%).

The registry lists serious adverse events for the 5.6 mg/kg group as 90 among 225 participants at risk and for the up-titration group as 16 among 50 at risk. The corresponding figures for other adverse events are 223 among 225 and 49 among 50. Death counts are listed as 114 and 28, respectively. These are group-level counts in the registry record; they are not, by themselves, evidence that an event was caused by treatment.

The most frequently listed serious-event terms include disease progression at 8.0%, pneumonitis and pleural effusion at 4.0% each, anaemia at 2.7%, and pneumonia and nausea at 2.2% each. The record does not provide further details about event timing, recurrent events, severity grades, attribution, or the definition used for each listed term. Serious-event counts should be read separately from the primary efficacy endpoint and with attention to the differing denominators. The registry record does not report a comparative safety analysis or uncertainty estimates for these figures.

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

The primary result describes the observed proportion of participants meeting a specific confirmed response definition in each treatment group. The risk difference and its confidence interval summarize the direction and uncertainty of the observed comparison. The lower observed response proportion in the up-titration group is a feature of these posted data, not a guarantee that the same difference would appear in another population or study.

The endpoint is response, not survival, duration of benefit, symptom improvement, or overall treatment effect. The registry lists some of these topics as secondary outcomes, but does not report analyses for most of them. The primary response result therefore cannot stand in for an overall assessment of all clinical outcomes. Likewise, response counts do not establish how individual participants experienced treatment or what happened to each participant outside the response classification.

The randomized design supports a comparison between the assigned regimens, but the registry record is not a complete account of the analysis. The study was open-label, although the primary endpoint was assessed by BICR. The record does not describe the allocation procedure, missing-data methods, analysis details, or multiplicity plan. Those omissions make it difficult to evaluate all potential sources of bias and the intended inferential framework from the registry information alone.

The findings should not be interpreted as proof that one regimen is clinically preferable. The reported confidence interval and unadjusted p-value are statistical summaries, not measures of clinical importance. The record does not state a threshold for a clinically meaningful difference, and no such threshold can be inferred from the observed result. Nor does the registry record establish that the posted results apply to people outside the described, previously treated EGFR-mutated NSCLC population.

In short, the posted numbers show the recorded BICR response counts and an unadjusted comparison for the two regimens. They do not, on their own, resolve the broader balance of efficacy, durability, survival, and safety, or provide the detailed analytical context needed for a complete evaluation.

17. Why This Trial Matters Statistically

Statistically, HERTHENA-Lung01 illustrates the difference between a trial’s named endpoint and the complete evidence needed to interpret it. The primary outcome has a clear operational definition: confirmed complete or partial response by BICR under RECIST v1.1. That definition allows the posted counts to be understood as a particular participant-level response measure rather than a general claim about disease course.

The comparison also shows why an effect estimate should be considered alongside its uncertainty. The risk difference provides a direct contrast in proportions, while its confidence interval indicates a range of values compatible with the data under the calculation method. A point estimate alone would conceal the uncertainty associated with the smaller up-titration analysis group. The registry also presents relative effect measures, which describe the same data on different scales and should not be mistaken for separate evidence.

The study’s open-label design and blinded central response assessment are distinct design features. Blinded review is relevant to an imaging-based primary endpoint, but the registry record does not include enough detail to assess the review process or the full protection against bias. This distinction is useful when considering how endpoint assessment and treatment masking relate to one another.

Finally, the registry’s mix of posted primary results and unreported secondary analyses illustrates the limits of relying on endpoint lists alone. The record identifies many outcomes, yet analyses for most are not reported. Information about multiplicity, missing data, analysis populations, and the original sample-size rationale is also absent. These features matter because a numerical result is most informative when its endpoint definition, population, analysis choices, and uncertainty can all be assessed together.

18. Limitations

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

The registry record leaves several trial-specific details unresolved. It does not describe the randomization method, allocation concealment, stratification, or the full conduct of the up-titration regimen. Although the study is described as randomized and open-label, those labels do not provide the operational detail needed to evaluate every aspect of treatment assignment and conduct.

The primary response assessment is assigned to BICR, but the registry does not report the review procedures, handling of disagreements, or whether imaging assessments were missing or unevaluable. The Efficacy Analysis Set is named without a full definition. The relationship between that population and all randomized participants is not explained, and missing-data rules and sensitivity analyses are not reported.

The registry reports an unadjusted comparison, but does not provide the complete statistical analysis plan, a multiplicity procedure, or details of any covariate-adjusted analysis. It also does not report a sponsor-reported comparative analysis in the listed analyses. The sample-size illustration uses the observed effect and specified planning assumptions; it is not evidence of the original design rationale, which is not reported in the registry record.

Most secondary outcomes are listed without reported analyses. For that reason, the record does not permit a full account of response durability, progression, survival, tumor change, or the secondary safety outcomes. The adverse-event summary provides counts and selected serious-event terms, but does not provide detailed event timing, attribution, severity, or comparative uncertainty. These limitations concern what can be concluded from the registry record; they do not establish that the study lacked procedures or analyses that are not reported there.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: HERTHENA-Lung01: Patritumab Deruxtecan in Subjects With Metastatic or Locally Advanced EGFR-mutated Non-Small Cell Lung Cancer — NCT04619004.
• Registry record last updated 2026-11-02; status last verified 2026-10.
• Results first posted 2024-04-02.
• 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.

22. Record Summary

HERTHENA-Lung01 (NCT04619004) is a randomized, open-label, parallel-group Phase 2 study of patritumab deruxtecan in previously treated metastatic or locally advanced EGFR-mutated NSCLC. Participants were assigned to a fixed 5.6 mg/kg regimen or an up-titration regimen, both administered intravenously every 3 weeks.

The primary endpoint is BICR-assessed ORR under RECIST v1.1 in the Efficacy Analysis Set. The registry posts response counts of 64 among 225 in the fixed-dose group and 8 among 50 in the up-titration group, with an unadjusted risk difference of -0.124 and a 95% confidence interval from -0.242 to -0.007. Most listed secondary outcomes have no reported analyses. Details of the original sample-size rationale, missing-data approach, and multiplicity strategy are not reported in the registry record.