Trastuzumab Deruxtecan (T-DXd) Alone or in Sequence With THP, Versus Standard Treatment (ddAC-THP), in HER2-positive Early Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trastuzumab Deruxtecan (T-DXd) Alone or in Sequence With THP, Versus Standard Treatment (ddAC-THP), in HER2-positive Early Breast Cancer (NCT05113251), a randomized phase 3 study. The primary outcome is Rate of Pathologic Complete Response (pCR)..

2. Clinical Question

The posted arm results report pathologic complete response for Arm A, Arm B, and Arm C. The recalculated comparisons contrast Arm B and Arm C separately with Arm A. The registry also reports sponsor analyses comparing Arm A with Arm C and Arm B with Arm C, using Miettinen and Nurminen's method. These comparisons address different pairs of arms, so their estimates should be read with their corresponding group labels rather than treated as interchangeable.

The trial is randomized and open-label. Random allocation supports comparisons between assigned strategies, while the lack of masking means participants and study personnel were not blinded to treatment assignment. The registry record does not report enough detail to establish how other aspects of care or outcome assessment were managed beyond the stated central evaluation of the primary endpoint.

3. Trial Design

DESTINY-Breast11 is a Phase 3 randomized, open-label, parallel-group trial with Arm A, Arm B, and Arm C. The registry lists an enrollment of 927 and describes the population as participants with high-risk, HER2-positive early-stage breast cancer. The trial is active, not recruiting. The primary completion date is 2025-03-12, and the record gives a primary pCR data cutoff of 12MAR2025, with assessment through definitive surgery or discontinuation or withdrawal and a maximum timeframe of approximately 40 months from randomization.

Arm A received trastuzumab deruxtecan alone. Arm B received trastuzumab deruxtecan followed by THP. Arm C received doxorubicin and cyclophosphamide followed by THP, corresponding to ddAC-THP in the title. The design therefore compares an experimental monotherapy strategy and a sequence beginning with T-DXd against a standard treatment sequence. It does not isolate the effect of each individual component from the effects of sequence or combination.

The primary outcome is the rate of pathologic complete response, expressed as a percentage of participants. The registry defines this as no evidence of residual invasive disease in the complete resected breast specimen and all sampled regional lymph nodes, using ypT0/Tis ypN0 by central evaluation following neoadjuvant therapy. Event-free survival count and event-free survival duration are listed as secondary outcomes.

Randomization is relevant because treatment assignment is not chosen solely by participants or clinicians, reducing some sources of systematic differences between groups. Open-label conduct does not itself show that the endpoint assessment was biased; the stated central evaluation provides information about assessment, but further masking details are not reported in the registry record. The record does not report the original design assumptions, sample-size justification, planned interim analyses, or the full statistical analysis plan.

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: Eligible patients had histologically documented human epidermal growth factor receptor 2 (HER2) - positive early stage breast cancer. Eligible patients were randomized in a 1:1:1 ratio using an interactive response technology (IRT) to receive either Arm A: Trastuzumab deruxtecan (T-DXd), Arm B: Trastuzumab deruxtecan followed by Paclitaxel + trastuzumab + pertuzumab (T-DXd-THP) or Arm C: Doxorubicin + cyclophosphamide followed by Paclitaxel + trastuzumab + pertuzumab (ddAC-THP).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full 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: This population includes all randomized patients.

6. Primary Endpoint

The registry lists the primary outcome as Rate of Pathologic Complete Response (pCR)., measured over Through to definitive surgery or discontinuation/withdrawal from study, up to a maximum of approximately 40 months from randomization to primary pCR DCO (12MAR2025).

The primary endpoint is the rate of pathologic complete response (pCR), reported as a percentage of participants. A participant meets the endpoint definition when there is no residual invasive disease in the complete resected breast specimen and all sampled regional lymph nodes. The registry specifies the pathology classification ypT0/Tis ypN0 and says that the endpoint is evaluated centrally after completion of neoadjuvant therapy.

pCR is used as a direct measure of the pathological response observed at surgery after treatment before surgery. It captures findings in both the breast and sampled regional lymph nodes, rather than relying only on change in tumour size or a clinical examination. The endpoint is binary at the participant level: each participant either meets the stated definition or does not. The posted rate describes the proportion meeting that definition in each arm.

This endpoint is not the same as a longer-term outcome. Event-free survival count and duration are listed as secondary outcomes, but the primary endpoint results alone do not establish what happens over longer follow-up. The registry describes the pCR assessment period as extending through definitive surgery or discontinuation or withdrawal from study, with a maximum of approximately 40 months from randomization to the primary pCR data cutoff. Further details on endpoint handling for participants without an evaluable surgical specimen are not reported in the registry record.

7. Results Posted in the Registry

• Arm B: 67.3% (216/321) versus 43.0% (123/286) on control; risk difference 24.3 percentage points (95% CI 16.6 to 32.0), risk ratio 1.56 (1.34–1.82); unadjusted two-proportion z-test p = <0.001.
• Arm C: 56.2% (180/320) versus 43.0% (123/286) on control; risk difference 13.2 percentage points (95% CI 5.3 to 21.1), risk ratio 1.31 (1.11–1.54); unadjusted two-proportion z-test p = 0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: pCR is either met or not met under the registry definition. For a binary outcome, an arm's event proportion is the number meeting the endpoint divided by the number assessed in the relevant analysis population. The posted percentages are arm-level proportions. Comparisons can be expressed in several ways, including a risk difference, risk ratio, or odds ratio. Each describes the same underlying outcome using a different scale, so the estimate must be interpreted according to its measure.

What does the risk difference mean?

A risk difference subtracts one group's event proportion from the other group's event proportion. A value of zero corresponds to equal proportions under that contrast. Positive or negative values indicate the direction of the contrast according to the group ordering. The recalculated estimates are reported as 0.243 for Arm B versus Arm A and 0.132 for Arm C versus Arm A. The calculations use the posted summary counts and are simple, unadjusted comparisons. The risk difference is often useful because it is an absolute contrast on the proportion scale, rather than a relative comparison.

The registry also lists risk ratios and odds ratios with confidence intervals for the recalculated comparisons. A risk ratio compares proportions by division; an odds ratio compares the odds of the outcome. These measures can give a different numerical impression from a risk difference, particularly when outcomes are common. They are not interchangeable with an absolute difference, and none should be treated as a causal effect without considering the design, analysis population, outcome definition, and potential biases.

How should the p-values be read?

The recalculated p-values are unadjusted: <0.001 for Arm B versus Arm A and 0.001 for Arm C versus Arm A. In general, a p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that the finding will replicate. Because the p-values are unadjusted, they do not account for the possibility of multiple statistical comparisons. The registry's complete multiplicity strategy is not reported.

The registry's own analyses are reported separately using Miettinen and Nurminen's method, with an estimate of the difference in rates, a confidence interval, and a p-value for each named pair. This method is designed for comparing binomial proportions and provides an inferential estimate and interval for the difference. The sponsor's group pairs are Arm A with Arm C, and Arm B with Arm C. The recalculated contrasts instead compare Arm B with Arm A and Arm C with Arm A. Since the pairs differ, numerical discrepancies between estimates are not by themselves evidence of a calculation error. The sponsor's reported analysis and the simple re-calculation answer distinct specified comparisons.

What does a confidence interval add?

A confidence interval describes uncertainty around an estimated contrast under a statistical procedure. In general, a 95% confidence interval is produced by a method that, over repeated comparable studies under its assumptions, would cover the target parameter at the stated rate. It is not a guarantee that the true value lies in the interval for this particular study. The endpoints show values reasonably compatible with the data and model, while the width reflects statistical precision. The intervals for the recalculated differences are 0.166 to 0.320 for Arm B versus Arm A and 0.053 to 0.211 for Arm C versus Arm A.

Confidence intervals depend on the analysis method and data included. The sponsor's Miettinen and Nurminen intervals need not match intervals produced by another method, even when the underlying outcome counts are similar. The posted summary does not provide confidence intervals around each standalone arm percentage. Therefore, precision for the arm-specific rates cannot be assessed from a rate interval in this record, although precision for the reported pairwise contrasts can be described.

Why distinguish the analysis population and endpoint process?

The primary outcome is stated for the full analysis set. The exact operational definition of that set, and the handling of participants without a post-treatment surgical assessment, are not reported in the registry record. Those details matter because exclusions, missing outcome data, and the timing of assessment can affect a binary proportion. Central evaluation is specified for the pathology assessment, but the record does not give further details about adjudication, blinding of assessors, or handling of disagreements.

The posted analysis is a snapshot tied to the stated primary data cutoff. It should not be assumed to include later follow-up or to represent a final account of secondary outcomes. Event-free survival count and duration are listed as secondary outcomes, but their detailed results and analysis methods are not included in the primary endpoint information summarized in the record.

What is general about the statistical explanation?

The explanations of risk differences, confidence intervals, p-values, and analysis assumptions are general statistical descriptions. The trial-specific estimates and named methods are those recorded for this study. The original sample-size calculation, planned model specifications, covariate adjustments, interim monitoring, and handling of multiplicity are not reported in the registry record, so they cannot be inferred from the posted results.

10. Confidence Intervals and Precision

The recalculated risk difference for Arm B versus Arm A is 0.243, with a 95% confidence interval from 0.166 to 0.320. For Arm C versus Arm A, the estimate is 0.132, with a 95% confidence interval from 0.053 to 0.211. Both intervals lie above zero, indicating that the observed data are compatible with positive differences on the risk-difference scale under the re-calculation method. The interval for Arm B versus Arm A is wider in absolute scale than the interval for Arm C versus Arm A; interval width reflects uncertainty as well as the scale and method used.

In general, a confidence interval is not a range containing a known fraction of individual participant outcomes. It quantifies uncertainty about an estimated population contrast under a statistical procedure. A narrower interval indicates greater statistical precision under that procedure, but precision is not the same as clinical importance or freedom from bias. The confidence intervals do not account for every possible uncertainty, such as limitations in endpoint ascertainment, missing-data handling, or multiplicity, unless the analysis explicitly incorporates those factors.

The registry reports sponsor-method intervals for different comparisons: -20.84 to -5.41 for Arm A versus Arm C, and 3.95 to 18.28 for Arm B versus Arm C. These are Miettinen and Nurminen intervals around the sponsor's stated difference-in-rates estimates. They should be interpreted with those group orderings and not substituted for the recalculated Arm B versus Arm A and Arm C versus Arm A intervals. Standalone confidence intervals for the three arm-specific pCR percentages are not reported in the registry record.

11. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, rather than the trial's original design calculation. For this binary endpoint, the entries are participants per arm. The underlying assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios use the stated fraction of the observed effect: 100%, 75%, or 50%. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planning number of participants per arm for a design with an 80% chance of detecting the assumed effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance of detection. In general, a design targeting higher power requires more participants when the other assumptions are unchanged. Likewise, smaller effects need more participants to detect reliably than larger effects, which is why the planning values increase for the smaller fractions of the observed effect.

For Arm B versus Arm A, the entries are 65 participants per arm for 80% power and 87 for 90% power when planning for 100% of the observed effect. Planning for 75% gives 117 and 157, while planning for 50% gives 265 and 355. For Arm C versus Arm A, the corresponding entries are 223 and 298 at 100%, 396 and 530 at 75%, and 890 and 1,190 at 50%.

These figures are not observed power. They are illustrative planning calculations based on the observed effect and stated assumptions, and they should not be read as the sample size used to design the trial or as evidence that the study had a particular probability of success.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.430; treatment proportion p₁ = 0.673; average p̄ = 0.551.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7033 = 1.3785.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6821 = 0.5740.
4. n = (1.3785 + 0.5740)² / (0.2428)² = 64.7, rounded up to 65 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 <- 0.43006993006993                          # control proportion
p1 <- 0.672897196261682                          # 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(5113251)
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 = 65 (80% power), 87 (90% power)
 75% of observed effect: n per arm = 117 (80% power), 157 (90% power)
 50% of observed effect: n per arm = 265 (80% power), 355 (90% power)
power.prop.test: 64.7 
Simulated power at n = 65 per arm: 0.794 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor reports two analyses using Miettinen and Nurminen's method. For Arm A versus Arm C, the estimate of the difference in rates is -13.18, with a 95% confidence interval from -20.84 to -5.41 and p=0.001. For Arm B versus Arm C, the reported estimate is 11.17, with a 95% confidence interval from 3.95 to 18.28 and p=0.003. The sign of a difference depends on group ordering, so the recorded pair and parameter definition are essential to reading each estimate.

The simple re-calculations use posted summary statistics and compare Arm B with Arm A, and Arm C with Arm A. They give risk differences of 0.243 and 0.132, respectively, with their own confidence intervals and unadjusted p-values. These are not the same contrasts as the sponsor's Arm A versus Arm C and Arm B versus Arm C analyses. The sponsor's method also differs from the simple unadjusted re-calculation, so exact numerical agreement is not expected across different pairs or methods.

The registry record does not report enough of the full statistical analysis plan to determine all prespecified details behind these analyses. The sponsor results should be read as the analyses the registry reports, while the re-calculated results are supplementary, unadjusted comparisons rather than a replacement for the sponsor's analysis.

14. Multiplicity, Missing Data and Analysis Populations

The record lists primary pCR and secondary event-free survival outcomes, and it reports multiple pairwise analyses of pCR. The recalculated p-values are unadjusted. The registry does not report a multiplicity adjustment for these comparisons or a hierarchy specifying which comparisons were intended to support confirmatory conclusions. Without that information, the nominal p-values should not be interpreted as if they necessarily control the overall false-positive risk across every analysis.

The sponsor's reported p-values are 0.001 for Arm A versus Arm C and 0.003 for Arm B versus Arm C. The record identifies Miettinen and Nurminen's method for these analyses, but does not state whether those tests were adjusted for multiple comparisons. The methods and pairings should be kept distinct from the supplementary re-calculated contrasts against Arm A.

The primary analysis population is named as the full analysis set. Further details defining that set are not reported in the registry record. The record also does not report how participants with missing pCR assessments, absent surgical specimens, treatment discontinuation, or withdrawal were handled in the analysis. These details are important for a binary outcome because the numerator and denominator can depend on the rules for unavailable or unevaluable outcomes.

The endpoint timeframe allows assessment through definitive surgery or discontinuation or withdrawal, up to a maximum of approximately 40 months from randomization to the stated primary pCR data cutoff. The record does not describe the precise censoring or imputation rules, nor whether sensitivity analyses were performed for missing outcome data. It also does not report interim analyses or stopping rules. These omissions do not establish that such procedures were absent; they mean that they are not reported in the registry record.

Randomization and the full analysis set provide important context, but they do not by themselves resolve every question about missing data, analysis populations, or multiplicity. A complete statistical analysis plan would be needed to assess those choices in detail.

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: pneumonia (2.9%), pneumonitis (2.2%), febrile neutropenia (2.2%), anaemia (1.6%), myelosuppression (1.6%).

The adverse-event record gives serious adverse events, other adverse events, and deaths by safety group. For T-DXd, the serious adverse-event counts are 29 among 283 at risk, other adverse events are reported for 269 among 283 at risk, and deaths are 8. For T-DXd-THP, the corresponding entries are 34 among 320 at risk, 306 among 320 at risk, and 3 deaths. For ddAC-THP, the entries are 63 among 312 at risk, 307 among 312 at risk, and 9 deaths.

These counts describe events recorded in the safety groups; they are not pCR results and do not establish that treatment caused an event. The registry lists pneumonia at 2.9%, pneumonitis at 2.2%, febrile neutropenia at 2.2%, anaemia at 1.6%, myelosuppression at 1.6%, and neutropenia at 1.6% among the top serious adverse-event terms. The record does not provide further detail alongside these terms in this summary about their specific denominators or event timing.

Read the at-risk counts alongside the affected counts when comparing groups. A count alone does not account for the number at risk, duration of observation, or the definition used for an event. The registry record does not report additional exposure-adjusted analyses or enough detail to compare event timing and severity across treatment strategies.

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

The posted results show that the pCR percentages differ across the randomized treatment arms: 43.01% for Arm A, 67.29% for Arm B, and 56.25% for Arm C. The recalculated contrasts indicate higher observed pCR proportions for Arm B and Arm C than for Arm A, with the stated confidence intervals and unadjusted p-values. The sponsor's reported analyses compare other arm pairs and use Miettinen and Nurminen's method. Each set of estimates should be interpreted on its own terms.

These results concern a defined pathological response after neoadjuvant therapy, assessed centrally using the stated ypT0/Tis ypN0 criteria. They do not, by themselves, demonstrate a difference in event-free survival, long-term outcomes, or any other endpoint. Event-free survival count and duration are listed as secondary outcomes, but the primary pCR results should not be treated as a substitute for those outcomes.

A statistically distinguishable difference is not automatically a clinically important difference. The confidence intervals describe statistical uncertainty for the stated contrasts, not the full range of uncertainty about how results may apply to other populations, settings, or treatment practices. The open-label design, the endpoint and analysis definitions, and the unavailable details about missing data and multiplicity all matter when interpreting the findings.

The results also do not predict whether an individual participant will achieve pCR, nor do they establish an individual's balance of benefits and harms. Arm-level proportions describe group outcomes. The safety counts provide separate information about adverse events and deaths, but do not by themselves establish causation or provide a complete comparison of safety over time.

Accordingly, the posted statistics support a description of observed pCR rates and specified pairwise contrasts in this trial population. They do not establish broader treatment conclusions beyond the endpoint, population, and analysis details reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative because it randomizes participants among distinct neoadjuvant treatment sequences and reports a binary pathological endpoint across the assigned arms. The treatment strategies differ in both drug components and sequence, making the estimand a comparison of strategies rather than a clean estimate of any single drug's isolated effect. That distinction is important when translating a group contrast into a scientific question.

The results also illustrate why the comparison being estimated matters. The simple recalculations contrast Arms B and C separately with Arm A, whereas the sponsor reports Arm A versus Arm C and Arm B versus Arm C. The direction and size of an estimate depend on the groups being compared and their order. Readers should identify the exact pair and method before interpreting a risk difference or p-value.

Reporting confidence intervals alongside estimates helps distinguish the magnitude of an observed contrast from the uncertainty around it. The sample-size illustrations show how planning requirements vary when the target effect is made smaller or the desired power is higher. Because those illustrations use the observed effect and specified assumptions, they are useful for understanding design trade-offs but do not reconstruct the trial's original design rationale.

The record also demonstrates the boundaries of what can be concluded from endpoint results alone. pCR is a defined pathological response, while event-free survival is a separate outcome. Missing-data rules, multiplicity procedures, the original design assumptions, and parts of the analysis plan are not reported. Identifying these gaps is part of sound statistical interpretation, not a claim that the analyses were necessarily inadequate.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The public record provides arm-level pCR percentages and pairwise analyses, but does not report confidence intervals for the standalone arm percentages. The sponsor analyses and the simple re-calculations use different pairings and methods, so they should not be treated as duplicate estimates of the same contrast. The record does not provide the full statistical analysis plan needed to establish the prespecified status of every comparison or the adjustment, if any, for multiplicity.

The full analysis set is named, but its operational definition is not reported in the registry record. Rules for missing or unevaluable pCR outcomes, withdrawals, and participants without definitive surgery are also not reported. This makes it difficult to independently assess the effect of missing outcome data on the posted percentages.

The trial is open-label. Central evaluation of the pathology endpoint is specified, but further information about assessor masking, adjudication, and quality-control procedures is not reported. Open-label conduct is not evidence that the endpoint was biased, but it is relevant context when evaluating trial procedures.

The original sample-size assumptions, sample-size justification, planned interim analyses, stopping rules, and detailed modeling choices are not reported. The posted planning illustrations are based on the observed effect and cannot be used to infer those original design decisions. The registry lists event-free survival as a secondary outcome, but the primary pCR information does not establish results for that longer-term endpoint.

Finally, the adverse-event summary gives counts and selected serious-event terms, but does not provide exposure-adjusted comparisons or full detail on timing and duration in this record. Safety counts should therefore be read as descriptive registry results rather than a complete causal comparison.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Trastuzumab Deruxtecan (T-DXd) Alone or in Sequence With THP, Versus Standard Treatment (ddAC-THP), in HER2-positive Early Breast Cancer — NCT05113251.
• Registry record last updated 2026-08-11; status last verified 2026-08.
• Results first posted 2026-06-09.
• 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

NCT05113251, DESTINY-Breast11, is a Phase 3 randomized, open-label, parallel-group trial of neoadjuvant treatment strategies for high-risk HER2-positive early breast cancer. It compares T-DXd alone, T-DXd followed by THP, and ddAC followed by THP. The registry lists enrollment of 927 and identifies pCR rate as the primary outcome, assessed by central evaluation using the ypT0/Tis ypN0 definition.

The posted pCR percentages are 43.01% for Arm A, 67.29% for Arm B, and 56.25% for Arm C. The registry reports sponsor analyses for Arm A versus Arm C and Arm B versus Arm C using Miettinen and Nurminen's method. Supplementary unadjusted recalculations compare Arms B and C separately with Arm A. The record also lists event-free survival count and duration as secondary outcomes and provides adverse-event counts by safety group.

Details about the original design assumptions, multiplicity procedures, missing-data handling, and full analysis plan are not reported in the registry record.