BI 836845 in Estrogen Receptor Positive Metastatic Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BI 836845 in Estrogen Receptor Positive Metastatic Breast Cancer (NCT02123823), a randomized phase 1 study. The primary outcome is Progression-free Survival (PFS) - Phase II Part.

2. Clinical Question

The clinical question is about the added treatment component, not a comparison of the complete regimens with no treatment. The registry describes a study in women with locally advanced or metastatic breast cancer, and its brief summary specifies HR-positive/HER2-negative advanced disease. Further eligibility details are not reported in the registry record.

The study title describes a phase Ib/II randomised study, while the registry phase field lists PHASE1. The posted primary comparison is specifically labelled as the phase II part. This distinction matters: dose-finding and dose-selection aims described for the broader study are not the same question as the phase II comparison of PFS.

The primary outcome concerns the interval from randomisation to a defined event, rather than tumour response at a single assessment. Its interpretation depends on the event definition, follow-up, and handling of people without a recorded event by the cut-off. The registry defines the endpoint and cut-off, but some details of missing-data and censoring methods are not reported in the registry record.

3. Trial Design

The registry describes a randomised, parallel-group study with no masking. It records the study as completed, with enrollment of 164. The listed start date is 2014-05-15 and the primary completion date is 2016-11-25. The official title describes a phase Ib/II study; the registry phase field lists PHASE1, while the posted primary outcome and comparison concern the phase II part.

The phase II experimental group received xentuzumab 1000 mg with everolimus 10 mg and exemestane 25 mg. Xentuzumab was administered by intravenous infusion once a week on specified days in a 28-day course; the accompanying oral drugs were described as daily. The comparator received everolimus 10 mg and exemestane 25 mg. Treatment was described as continuing until disease progression, intolerable adverse events, or another reason requiring withdrawal. The full dosing description for the experimental group is truncated in the registry record.

The primary analysis used the randomised set: all phase II participants assigned to a group, regardless of whether they received treatment. The posted group sizes for the PFS outcome are 70.0 in each arm. The registry defines PFS from randomisation until radiological tumour progression according to RECIST 1.1 or death from any cause, whichever occurred earlier.

At the 25Nov2016 cut-off, the sponsor discontinued xentuzumab in all participants in the experimental arm and recruitment was terminated. Participants who stopped xentuzumab continued everolimus and exemestane. This change is relevant to interpreting follow-up and exposure; it does not alter the stated randomised comparison. The reason for the sponsor decision and further details of the decision process are not reported in the registry record. Allocation concealment, the randomisation sequence procedure, and the original design assumptions are also 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: Only subjects that met all inclusion + none of exclusion criteria were to be entered. Subjects were free to withdraw from clinical trial at any time for any reason given. If subject continued to take trial drug, close monitoring was adhered to + adverse events recorded. Rules were implemented in all trials whereby doses would be reduced if required. If further events were reported, subject would be withdrawn from trial. Symptomatic treatment of tumor associated symptoms were allowed throughout.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomised set (RS): This patient set included all randomised patients in the Phase II part, regardless of whether or not they received treatment. Patients were assigned to xentuzumab (BI 836845) in combination with exemestane and everolimus or exemestane and everolimus alone as randomised.

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: Treated set (Phase Ib only): This patient set included all patients who were documented to have received and taken at least one dose of any study medication during the treatment cycles (from Day 1). Randomised set (RS) (Phase II only): This patient set included all randomised patients in the Phase II part, regardless of whether or not they received treatment. Patients were assigned to xentuzumab in combination with exemestane and everolimus or exemestane and everolimus alone as randomised.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS) - Phase II Part, measured over From randomisation until radiological tumour progression according to RECIST 1.1, or death from any cause or data cut-off (25Nov2016), up to 30 months..

Progression-free survival measures the time from randomisation until the first of radiological tumour progression or death from any cause. The registry specifies tumour progression according to RECIST 1.1 and says clinical progression was not counted as a PFS event unless it led to death. Follow-up was considered through the data cut-off of 25Nov2016, with the stated timeframe extending up to 30 months.

A time-to-event endpoint retains information about when events occur, rather than reducing follow-up to a simple count of participants with or without an event. The median is the time by which half of the analysed group is estimated to have experienced the event, under the survival-analysis framework. It is a summary of the event-time distribution, not a statement that every participant had an event at that time.

PFS is used in trials because it combines progression and death into a defined outcome and can describe the course of disease during follow-up. Its meaning depends on consistent assessment and clear event and censoring rules. The registry gives the event definition, but detailed assessment schedules, censoring rules, and methods for handling missing assessments are not reported in the registry record.

The posted medians are 7.3 months for the xentuzumab group and 5.6 months for the comparator. The corresponding confidence interval for the xentuzumab median has a lower limit of 3.3 months; its upper limit is not reported. The comparator interval is 3.7 to 9.1 months. These arm summaries do not by themselves quantify the relative hazard over follow-up; the reported hazard ratio addresses that comparative time-to-event question.

7. Results Posted in the Registry

• Xentuzumab (BI 836845) 1000 mg + Everolimus 10 mg + Exemestane 25 mg - Phase II vs Everolimus 10 mg + Exemestane 25 mg - Phase II: hazard ratio 0.97 (95% CI 0.57–1.65), reported p = 0.906 (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.

Number of Patients With Objective Response (OR) - Phase II Part

• 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:
  • Everolimus 10 mg + Exemestane 25 mg - Phase II: 10.0% (7/70) versus 7.1% (5/70) on control; risk difference 2.9 percentage points (95% CI -6.4 to 12.1), risk ratio 1.40 (0.47–4.20); unadjusted two-proportion z-test p = 0.546.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Everolimus 10 mg + Exemestane 25 mg - Phase II and the control. The interval gives the range of effects that remain compatible with the data.

Time to Progression (TTP) - Phase II Part

• 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:
  • Xentuzumab (BI 836845) 1000 mg + Everolimus 10 mg + Exemestane 25 mg - Phase II vs Everolimus 10 mg + Exemestane 25 mg - Phase II: hazard ratio 1.03 (95% CI 0.59–1.80), reported p = 0.915 (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 Xentuzumab (BI 836845) 1000 mg + Everolimus 10 mg + Exemestane 25 mg - Phase II vs Everolimus 10 mg + Exemestane 25 mg - Phase II and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients With Disease Control (DC) - Phase II Part

• 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:
  • Everolimus 10 mg + Exemestane 25 mg - Phase II: 24.3% (17/70) versus 18.6% (13/70) on control; risk difference 5.7 percentage points (95% CI -7.8 to 19.3), risk ratio 1.31 (0.69–2.48); unadjusted two-proportion z-test p = 0.410.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Everolimus 10 mg + Exemestane 25 mg - Phase II and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover objective response, time to progression, and disease control, alongside additional response-duration measures listed in the registry. The reported results for objective response and disease control do not show a clear statistical separation between the randomised groups, and the time-to-progression comparison likewise does not provide clear evidence of a group difference. The registry also lists time to objective response, duration of objective response, and duration of disease control, but their results are not reported in the registry record.

This broad pattern is consistent with the primary PFS analysis in the limited sense that the reported comparisons do not establish a clear advantage for either group. Secondary endpoints are not interchangeable with PFS: response counts describe tumour assessment categories, time to progression excludes death from its event definition, and response duration applies to a selected subset with an objective response. Differences in definitions and analysis populations mean that agreement or disagreement across endpoints should not be treated as a direct replication.

Secondary results generally carry less weight when many outcomes are examined without a reported adjustment for multiple comparisons. A collection of tests creates more opportunities for chance findings, while a non-significant result on one secondary outcome does not prove the absence of an effect. The registry does not report a multiplicity procedure or a prespecified hierarchy for interpreting secondary outcomes. These results are therefore best considered supportive and exploratory rather than decisive evidence about the primary question.

The reported logistic-regression odds ratios are the sponsor's analyses, while unadjusted summaries based on counts are simple recalculations. The choice of scale and method affects interpretation, so the odds ratios should not be translated directly into changes in probability. The overall reading should focus on the consistency and uncertainty of the estimates, not on selecting an isolated result from among several endpoints.

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

• Number of Patients With Objective Response (OR) - Phase II Part
• Time to Progression (TTP) - Phase II Part
• Number of Patients With Disease Control (DC) - Phase II Part
• Time to Objective Response - Phase II Part
• Duration of Objective Response - Phase II Part
• Duration of Disease Control - Phase II Part

9. Statistical Interpretation

10. Statistical Methods Explained

What does the hazard ratio describe?

For a time-to-event outcome, a hazard is the instantaneous event rate among people who have not yet had the event, conditional on remaining under observation up to that time. A hazard ratio compares these rates between groups. In the posted PFS analysis, the reported hazard ratio is 0.97. A value of 1 represents equal hazards under this comparison; values on either side indicate different relative rates. The hazard ratio does not directly report a difference in median months, nor does it mean that an individual participant's risk changes by that amount.

A hazard ratio is often interpreted under a proportional-hazards framework, in which the relative hazard is treated as sufficiently stable over time. The registry identifies a log-rank analysis and reports a hazard ratio, but does not report a proportional-hazards diagnostic or a full statistical analysis plan. If relative hazards vary over time, one summary hazard ratio may not capture all features of the survival curves. The plotted curves can help readers inspect the pattern, but visual inspection is not a formal test of model assumptions.

Why use the log-rank method?

The log-rank test compares observed event counts with counts expected under a no-difference hypothesis across event times. It is a common method for comparing time-to-event groups and uses follow-up information from participants who have not yet had an event, subject to censoring. The registry reports the PFS comparison using the log-rank method and gives p = 0.906. The p-value addresses compatibility with the no-difference hypothesis under the test's assumptions; it does not measure the size or clinical importance of an effect.

Censoring occurs when a participant's event time is not observed during the available follow-up, for example because observation ends before an event is recorded. Such observations still contribute information up to their last known follow-up under standard survival methods. The registry specifies the cut-off and event definition, but the detailed censoring rules and assumptions are not reported in the registry record. This limits independent assessment of how incomplete follow-up was treated.

What do the medians and intervals add?

The median PFS describes the estimated time at which the survival function reaches one half. It gives a time-scale summary that complements the hazard ratio. The posted medians are 7.3 months and 5.6 months. Confidence intervals convey uncertainty in the estimates. For the xentuzumab-group median, the posted lower limit is 3.3 months and the upper limit is not reported; for the comparator median, the interval is 3.7 to 9.1 months. A missing limit should not be inferred from the other statistics.

The median is not a complete description of the survival curve. Two groups can have similar medians but different patterns at other times, or different medians with uncertainty that prevents a firm comparative conclusion. For that reason, the reported hazard ratio and its interval should be considered alongside the medians rather than replaced by them.

How should the secondary analyses be understood?

The registry also posts participant counts for objective response and disease control, plus a median time-to-progression analysis. The response and disease-control comparisons use logistic regression in the reported analyses, which expresses the group contrast as an odds ratio. Odds are not the same as probabilities, and an odds ratio should not be read as a direct percentage-point change. The registry reports odds ratios and confidence intervals for these analyses.

For binary outcomes, an unadjusted comparison can be recalculated from the posted counts, but it is not the same as the sponsor's regression estimate. Such a recalculation does not account for model covariates and should be treated as a simple descriptive analysis. The sponsor's reported analysis is the trial's own analysis and takes precedence when describing the registry's inferential result. No discrepancy is flagged for the primary endpoint.

The secondary time-to-progression analysis also uses a log-rank method and reports a hazard ratio. Time to progression is not identical to PFS: the registry's TTP definition uses objective tumour progression, while PFS also counts death. This difference in endpoint definition matters when comparing results. The registry lists additional secondary outcomes, but results for time to objective response, duration of objective response, and duration of disease control are not reported in the registry record.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model assumes less variability than the data contain, standard errors can be too small and confidence intervals too narrow. This is a general statistical concern, not a reported feature of this trial. The registry does not report an over-dispersion assessment for these outcomes.

More broadly, the registry record does not report the original sample-size justification, a detailed analysis plan, interim analyses, or adjustment for multiple comparisons. These omissions mean that it is not possible to determine from the record whether the analysis methods or monitoring decisions followed a more detailed prespecified plan.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.97, with a 95% confidence interval from 0.57 to 1.65. A confidence interval describes the range of estimates compatible with the observed data and the statistical method, under its assumptions. It is not a range containing a known proportion of individual participants' outcomes, and it is not a probability statement about the true effect after the data have been observed.

Because the interval includes 1, the primary result is compatible with equal hazards as well as with relative hazards below or above that value. Its width indicates that the estimate is not precise enough to distinguish among a broad range of possible comparative effects. The p-value of 0.906 is consistent with the absence of a clear statistical separation in this analysis. Neither the interval nor the p-value establishes that the treatments are equivalent.

The group median estimates also have uncertainty. The comparator median interval extends from 3.7 to 9.1 months. For the xentuzumab median, the registry reports a lower limit of 3.3 months but does not report an upper limit. The absence of that limit should be treated as missing information rather than reconstructed from the other results.

Precision is affected by the number and timing of observed events, length and completeness of follow-up, and the analysis assumptions. The registry provides group sizes for the primary analysis, but detailed event counts and censoring information are not included in the listed results. The overall enrollment figure should not be substituted for the analysed phase II group sizes. Without further information about events and missing follow-up, the reasons for the observed interval width cannot be separated.

Confidence intervals for secondary outcomes are also broad, and the registry's several endpoint analyses increase the need for cautious interpretation. These intervals describe uncertainty for their respective estimates; they do not address the chance of at least one chance finding across multiple tests unless a multiplicity method is applied. Such a method is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect, with alternatives that plan for 100%, 75%, or 50% of that effect. For the binary secondary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events across the comparison, not participants per arm. The units therefore differ by outcome type, and figures should be read only alongside the corresponding endpoint.

The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show illustrative sample sizes or event totals for 80% or 90% power under those assumptions. In plain terms, the 80% power column gives the planning quantity associated with an 80% chance of detecting the specified effect if that effect and the assumptions are correct; the 90% column uses a higher chance of detection. These are design illustrations, not observed trial outcomes.

Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants or events. The figures are derived from the observed effect in this study and are not the trial's original design targets. The registry record does not report the original sample-size justification or its assumptions.

This is not observed power. It is a planning calculation using an assumed effect and specified statistical conditions, and it cannot establish the probability that the completed trial detected a real effect. The actual trial enrolled 164 overall, while the posted phase II PFS groups each contain 70.0; these should not be confused with the illustrative planning quantities.

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 = 0.970, so ln(HR) = -0.0305.
2. d = 4 × (1.96 + 0.842)² / [ln(0.970)]² = 33,840.0, rounded up to 33,841 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 <- 0.97                              # 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(2123823)
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 = 33,841 (80% power), 45,303 (90% power)
 75% of observed effect: events = 60,161 (80% power), 80,538 (90% power)
 50% of observed effect: events = 135,361 (80% power), 181,209 (90% power)
Simulated power with 33,841 events: 0.805 (20000 replicates)

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

14. Group-Sequential Design Analysis

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

Under these assumptions the design needs about 49,728 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 164 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 <- 5.6          # control-arm median, months (converted from the posted unit)
hr          <- 0.97          # 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: 29900         p (1-sided)   0.0001
 Events: 15279        ~HR at bound   0.9417
     Month: 14    P(Cross) if HR=1   0.0001
               P(Cross) if HR=0.97   0.0338
     IA 2: 67%                   Z   2.5114
      N: 48036         p (1-sided)   0.0060
 Events: 30558        ~HR at bound   0.9717
     Month: 23    P(Cross) if HR=1   0.0060
               P(Cross) if HR=0.97   0.5603
         Final                   Z   1.9930
      N: 49728         p (1-sided)   0.0231
 Events: 45837        ~HR at bound   0.9816
     Month: 60    P(Cross) if HR=1   0.0250
               P(Cross) if HR=0.97   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 sponsor's reported primary analysis is a log-rank hazard ratio of 0.97, with a 95% confidence interval from 0.57 to 1.65 and p = 0.906. The primary comparison in the record uses these reported values. The statistical recalculations associated with this analysis do not identify a discrepancy, so there is no conflicting recalculated primary estimate to reconcile.

For binary secondary outcomes, unadjusted calculations from posted counts can differ from the sponsor's logistic-regression estimates because they use different methods. The registry's own analyses report odds ratios from logistic regression for the response and disease-control outcomes. Those sponsor analyses are the appropriate figures to cite as the trial's reported inferential results; unadjusted recalculations are supplementary descriptions and do not replace them.

The registry does not report all details of covariate selection, model diagnostics, or the full statistical analysis plan. Consequently, the exact role of any model adjustments cannot be fully assessed from this record. This limitation does not alter which values were reported by the sponsor, but it constrains independent evaluation of the analytic choices.

16. Multiplicity, Missing Data and Analysis Populations

The record lists a primary PFS outcome and several secondary outcomes, with reported analyses for a subset of them. It does not report whether the trial used a formal multiplicity adjustment, a testing hierarchy, or another strategy to control the chance of false-positive findings across outcomes. Without that information, the secondary p-values should not be interpreted as if each were the only hypothesis tested.

Handling of missing outcome data is also not described in detail. The PFS population is defined as the randomised set, including assigned participants whether or not they received treatment. The record specifies the PFS event definition and the data cut-off, but does not report detailed censoring rules, procedures for missing tumour assessments, or sensitivity analyses for incomplete follow-up. Those omissions limit assessment of possible bias due to incomplete observation.

The phase II comparison is based on participants as randomised, which preserves the group assignment framework for the primary analysis. However, the record does not provide a complete account of protocol deviations, treatment adherence, or how post-discontinuation follow-up was incorporated. The sponsor discontinued xentuzumab and terminated recruitment at the cut-off; the stated continuation of everolimus and exemestane is relevant context, but does not answer all questions about later outcome ascertainment.

The original sample-size rationale, interim analyses, and full statistical analysis plan are not reported in the registry record. It is therefore not possible to establish whether the available analyses followed prespecified decision rules, whether any unreported outcome analyses were planned, or how missingness and multiplicity were anticipated. These are limits on what can be learned from the registry entry, not evidence that a particular procedure was or was not used.

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: malignant neoplasm progression (100.0%), febrile neutropenia (33.3%), pyrexia (9.5%), pneumonitis (7.2%), deafness (4.8%).

The registry reports serious adverse event figures separately for phase Ib and phase II groups. In phase II, serious adverse events affected 20 participants in the xentuzumab group, with 70 at risk, and 29 in the comparator group, with 69 at risk. Other adverse events affected 70 and 68 participants, respectively, among the stated at-risk groups. The record also reports deaths of 9 and 11 in those phase II groups. These counts describe the registry's safety listings and are not adjusted comparisons.

Phase Ib figures are reported separately: the 750 mg xentuzumab group had 3 at risk and 3 affected by serious adverse events; the 1000 mg group had 21 at risk and 10 affected. The record reports other adverse events for 3 and 21 participants in those groups, and deaths of 0 and 2. These early-phase groups should not be merged with the phase II comparison.

The listed serious-event terms include malignant neoplasm progression, febrile neutropenia, pyrexia, pneumonitis, deafness, and intestinal obstruction, with registry percentages attached to those terms. A serious adverse event is not necessarily caused by study treatment, and event counts do not by themselves establish a treatment-related difference. The registry record does not provide enough detail to assess causality, exposure-adjusted rates, or comparative safety statistically.

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

The primary result estimates the relative rate of progression or death in the two randomised phase II groups. The point estimate is close to 1, while its 95% confidence interval includes values both below and above 1. The data therefore do not establish a clear difference in PFS between xentuzumab plus everolimus and exemestane and everolimus and exemestane alone. The result should not be interpreted as proof that the regimens are identical.

The median PFS estimates provide a time-based description for each group, but do not replace the comparative hazard-ratio analysis. The reported uncertainty is substantial, and the upper confidence limit for the experimental median is not reported. Readers should retain that uncertainty rather than treating the medians as exact points or converting them into an unreported treatment effect.

The trial also does not establish from these registry results that xentuzumab has no effect, or that it has a beneficial effect. A non-significant comparison is not an equivalence finding, and no equivalence margin or non-inferiority objective is reported. The results apply to the study's defined phase II comparison and outcome; they should not be generalized beyond the population and treatment context described in the registry.

The sponsor stopped xentuzumab and recruitment at the stated cut-off. This is important context for treatment exposure and follow-up, but the registry does not report the reasons or full implications of the decision. It does not justify attributing the decision to a particular efficacy or safety finding. Similarly, the listed adverse-event counts cannot by themselves establish whether an event was caused by treatment.

Overall, the posted data are compatible with uncertainty about the relative PFS effect. They support a cautious description of the observed estimates, not a clinical recommendation. Decisions about individual care require evidence and clinical context beyond this statistical account.

19. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a group-specific median and a comparative time-to-event estimate. The median summaries suggest distinct time points, while the hazard ratio and its confidence interval describe the relative event pattern across follow-up and convey substantial uncertainty. Readers who focus only on the medians may overstate what the comparison establishes.

The registry also distinguishes the broader phase Ib/II study from its phase II randomised comparison. The phase Ib groups used different xentuzumab doses, while the posted primary question compares the 1000 mg phase II regimen with the control regimen. Keeping these parts separate avoids mixing dose-finding safety information with the primary efficacy comparison.

The sponsor's discontinuation of xentuzumab at the cut-off highlights how operational decisions can affect treatment exposure and follow-up. The randomised-set definition preserves an assignment-based comparison, but the available registry description does not resolve every question about post-discontinuation ascertainment. A careful reading separates what the record reports from explanations it does not provide.

Finally, the planning illustrations show why observed effects should not be mistaken for fixed design targets. Smaller effects require more participants or events under the stated assumptions, and the original sample-size rationale is not reported. Together, these features make the study a useful example of interpreting time-to-event estimates, uncertainty, analysis populations, and registry reporting limits without turning a non-significant result into a claim of equivalence.

20. Limitations

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

The registry record does not provide a full protocol or statistical analysis plan. Details of randomisation sequence generation and allocation concealment are not reported, nor are the original sample-size assumptions, interim analyses, or multiplicity procedures. This limits assessment of whether analysis and decision rules were prespecified.

The primary endpoint's general definition and cut-off are reported, but detailed censoring rules, handling of missing tumour assessments, and sensitivity analyses are not. The experimental median's upper confidence limit is also not reported. These gaps constrain interpretation of the survival estimates and independent checking of the analysis.

The sponsor stopped xentuzumab in the experimental group and terminated recruitment at the cut-off. Participants who stopped xentuzumab continued the other study drugs, but the registry does not give further detail on subsequent treatment, exposure, or follow-up. The effect of these circumstances on later outcome observation cannot be determined from the record.

Although the overall enrollment is 164, the primary phase II outcome lists groups of 70.0 each, and the safety denominator for the phase II comparator is 69. The registry does not explain the difference between these reported analysis sets. These figures should be kept in their stated contexts rather than reconciled by assumption.

The registry phase field lists PHASE1 while the title describes phase Ib/II and the posted primary analysis is labelled phase II. This record-level inconsistency is relevant context. Results for some listed secondary outcomes are not reported, limiting a complete assessment of the study's outcome pattern.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: BI 836845 in Estrogen Receptor Positive Metastatic Breast Cancer — NCT02123823.
• Registry record last updated 2025-07-15; status last verified 2025-06.
• Results first posted 2025-07-15.
• 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

NCT02123823 is a completed, randomised, open-label, parallel-group study sponsored by Boehringer Ingelheim. Its title describes BI 836845, also called xentuzumab, with everolimus and exemestane versus everolimus and exemestane alone in women with locally advanced or metastatic breast cancer. The registry phase field lists PHASE1; the posted primary outcome is for the phase II part.

The primary endpoint is PFS in the randomised set. The reported hazard ratio is 0.97, with a 95% confidence interval from 0.57 to 1.65 and p = 0.906. The interval includes 1 and leaves substantial uncertainty about the comparative effect. The registry lists secondary response, time-to-progression, and disease-control outcomes, as well as safety counts. Some listed secondary results and important design and analysis details are not reported in the registry record.