Comparing the Efficacy and Tolerability of Fulvestrant 500 mg Versus 250 mg in Advanced Breast Cancer Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing the Efficacy and Tolerability of Fulvestrant 500 mg Versus 250 mg in Advanced Breast Cancer Women (NCT01300351), a randomized phase 3 study. The primary outcome is Progression-free Survival.

2. Clinical Question

The clinical question concerns the relative timing of progression or death under the two randomized dose regimens in this trial population. Progression was defined using RECIST v1.1 criteria: a qualifying increase in the summed diameters of target lesions, unequivocal progression of existing non-target lesions, appearance of new lesions, or death from any cause in the absence of progression. The trial record also lists objective response, clinical benefit, duration of response, and duration of clinical benefit as secondary outcomes. These outcomes provide additional descriptions of tumor response and its duration, but they are not the primary endpoint.

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group, multicentre study sponsored by AstraZeneca. The registry lists an enrollment of 249 and a completed status. The recorded start was 2011-03 and primary completion was 2014-03. The population was postmenopausal women with ER+ advanced breast cancer after progression or relapse following previous endocrine therapy; the brief summary specifies Chinese women.

Participants were assigned to fulvestrant 500 mg or 250 mg. The higher-dose regimen used two fulvestrant syringes, while the lower-dose regimen used a fulvestrant syringe and a matching placebo syringe. Both regimens included monthly intramuscular injections and a day-14 first-month injection procedure. The record identifies placebo as an intervention, but the arm descriptions show it was used as matching placebo alongside active fulvestrant, not as a separate placebo-only comparison group.

The primary efficacy population was the FAS, defined as all randomized patients analyzed according to randomized treatment, regardless of treatment actually received. The primary endpoint timeframe was 36 months. The arm counts listed for the primary endpoint are 111 for fulvestrant 500 mg and 110 for fulvestrant 250 mg. The enrollment figure and endpoint arm counts describe different registry entries; the record does not explain the difference.

The record identifies the primary analysis as a log-rank test stratified by the last endocrine therapy received before fulvestrant, categorized as AO versus AI. It reports a hazard ratio with a 95% confidence interval and p value. The registry record does not report the original sample-size justification, detailed recruitment procedures, or whether interim analyses were planned or conducted. Those details should not be inferred from the enrollment or the later planning illustrations.

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: The Enrollment number in the protocol section means the number of patients enter the trial and receiving screening procedure, the number of participants Started in the Participant Flow module means the number of randomized patients and do not include screening failure patients.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS: all randomised patients and compared the treatment groups on the basis of randomised treatment, regardless of treatment actually received.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The planned population size was 220 randomised patients and altogether 221 patients were randomised. Key demographic and baseline characteristics were balanced between the treatment groups.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival, measured over 36 months.

Progression-free survival measures the time until disease progression or death, according to the endpoint definition used in the trial. Progression was defined by RECIST v1.1 criteria: at least a 20% increase in the sum of diameters of target lesions, using the smallest on-study sum as the reference; unequivocal progression of existing non-target lesions; appearance of new lesions; or death from any cause when progression had not occurred. The timeframe listed for this outcome is 36 months.

A time-to-event endpoint uses both whether an event occurred and when it occurred. That makes it different from a simple count of participants with progression by a fixed point: the analysis can incorporate varying follow-up and the ordering of events over time. The registry reports median progression-free survival of 8 months for fulvestrant 500 mg and 4 months for fulvestrant 250 mg, with interquartile ranges of 2.8 to 16.6 months and 2.7 to 11.1 months, respectively. The medians describe the midpoint of each group’s observed time-to-event distribution; they do not by themselves summarize the full comparison between groups.

The primary comparison instead uses a log-rank test and a hazard ratio. The hazard ratio describes the relative event rate over the analyzed follow-up under the model and analysis used. It should be read together with its confidence interval and p value, rather than treating the two medians as a complete measure of the treatment contrast.

7. Results Posted in the Registry

• Fulvestrant 500 mg vs Fulvestrant 250 mg: hazard ratio 0.75 (95% CI 0.54–1.03), reported p = 0.078 (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.

Objective Response Rate

• 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:
  • Fulvestrant 250 mg: 16.7% (11/66) versus 28.1% (16/57) on control; risk difference -11.4 percentage points (95% CI -26.1 to 3.3), risk ratio 0.59 (0.30–1.17); unadjusted two-proportion z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fulvestrant 250 mg and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Benefit Rate

• 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:
  • Fulvestrant 250 mg: 32.7% (36/110) versus 47.7% (53/111) on control; risk difference -15.0 percentage points (95% CI -27.8 to -2.2), risk ratio 0.69 (0.49–0.95); unadjusted two-proportion z-test p = 0.023.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Fulvestrant 250 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The available secondary results add information about response and clinical benefit, but they do not all point to the same level of statistical certainty. The sponsor’s objective-response analysis has a 95% confidence interval for the odds ratio that includes 1 and a p value of 0.107. The clinical-benefit analysis has a confidence interval that excludes 1 and a p value of 0.023. These outcomes therefore have different reported inferential patterns. They are not substitutes for the primary progression-free survival result, which is a time-to-event outcome with its own estimate and uncertainty.

The posted results also include simple unadjusted recalculations for the binary outcomes. Those calculations are based on group counts and use a different comparison from the sponsor’s logistic-regression odds ratios. They should be kept separate from the sponsor-reported results rather than blended into a single conclusion. In particular, an unadjusted p value is not a replacement for the sponsor’s model-based p value.

The registry lists objective response rate, clinical benefit rate, duration of response, and duration of clinical benefit as secondary outcomes. Quantitative results for the first two appear in the record; results for duration of response and duration of clinical benefit are not reported in the registry record. Across the secondary outcomes that do have numerical analyses, the findings offer additional context, but interpretation is limited by the number of outcomes and the absence of a reported multiplicity strategy.

When several secondary endpoints are tested, the chance of at least one apparently notable result can increase if the tests are interpreted without adjustment. That does not make a secondary result invalid, but it means that isolated p values generally carry less weight than a primary result whose role is defined in advance. The registry record does not report whether secondary endpoints were ordered hierarchically, adjusted for multiplicity, or treated as exploratory. The secondary results should therefore be understood as supportive descriptive evidence rather than as a replacement for the primary endpoint.

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

• Objective Response Rate
• Clinical Benefit Rate
• Duration of Response
• Duration of Clinical Benefit

9. Statistical Interpretation

10. Statistical Methods Explained

The main statistical result is a time-to-event comparison. For this kind of endpoint, participants contribute information through both their event status and the time at which an event is observed. A participant whose follow-up ends before an event may contribute information up to that point without being treated as if an event had occurred. The registry defines progression or death as the event for progression-free survival and reports a log-rank analysis.

What does the hazard ratio describe?

A hazard is the event rate at a particular time among participants who have not yet experienced the event. A hazard ratio compares the hazards between groups over follow-up, according to the analysis model. Here, the reported ratio is for fulvestrant 500 mg relative to fulvestrant 250 mg. A value below 1 is in the direction of a lower estimated hazard for the first group; a value above 1 is in the direction of a higher estimated hazard. This is a relative comparison, not a direct statement about how many participants experienced progression or how long any individual participant remained progression-free.

The estimate is 0.75, with a 95% confidence interval from 0.54 to 1.03. The interval describes the range of values reasonably compatible with the data and analysis under the assumptions of the method. Because it includes 1, it includes no relative hazard difference. It also includes values below and above 1, so the direction and size of the true relative difference remain uncertain. The reported p value is 0.078. A p value describes how unusual results at least as discrepant as the observed result would be under a null hypothesis and the analysis assumptions; it is not the probability that the null hypothesis is true.

Why use a log-rank test?

The log-rank test compares event-time experience across groups while taking account of event timing and censoring. Censoring occurs when an event time is not observed during a participant’s recorded follow-up; the participant can still contribute information while under observation. The registry states that the primary log-rank test was stratified by the last endocrine therapy before fulvestrant, categorized as AO versus AI. Stratification allows the comparison to account for those stated strata in the test. Further details of the implementation, including additional modeling choices, are not reported in the registry record.

The registry reports the hazard ratio and its confidence interval alongside the log-rank p value. These quantities answer related but different questions. The ratio estimates the relative contrast, the interval expresses its uncertainty, and the p value summarizes evidence against the null under the stated test. Reading them together avoids reducing the result to a single threshold judgment.

How do the medians and interquartile ranges fit in?

The median is the time by which half of the analyzed group’s event-time distribution has reached the event, under the way the distribution is estimated. The reported medians are 8 months and 4 months. The interquartile ranges are 2.8 to 16.6 months and 2.7 to 11.1 months. These summaries show the center and spread of the observed time distribution, but they do not tell the full story of the event-time curves or their uncertainty. In particular, the medians cannot be substituted for the hazard ratio, and their difference should not be treated as the complete time-to-event effect.

What do the secondary binary analyses estimate?

For objective response rate and clinical benefit rate, the sponsor reports logistic-regression odds ratios. An odds ratio compares the odds of the recorded outcome between groups; it is not the same quantity as a risk difference or a ratio of probabilities. Objective response was reported as 16 of 57 in the 500 mg group and 11 of 66 in the 250 mg group. Clinical benefit was reported as 53 of 111 and 36 of 110, respectively. The sponsor’s reported odds ratios and confidence intervals come from logistic regression, while the simple unadjusted recalculations in the posted results use summary counts. Differences in analysis approach can produce different estimates and p values; the sponsor’s own analysis takes precedence when describing the trial’s reported analysis.

For binary outcomes, confidence intervals represent uncertainty about the estimated contrast under the method used. A confidence interval that includes the null value for the reported measure does not establish that the groups are identical; it indicates that the data do not rule out the null value at that interval level. Conversely, an interval that excludes the null does not by itself establish clinical importance. The reported objective-response confidence interval for the odds ratio includes 1; the clinical-benefit confidence interval does not. These are secondary outcomes, and the record does not report a multiplicity adjustment that would address the interpretation of several outcome tests together.

General statistical context: over-dispersion matters when outcome variation is greater than a model’s assumed distribution allows. In such settings, standard errors can be too small if the extra variation is ignored. The registry record does not report an over-dispersion assessment or a model of that kind for the primary time-to-event analysis, so this general issue should not be read as a finding about this trial.

11. Confidence Intervals and Precision

The primary 95% confidence interval for the hazard ratio is 0.54 to 1.03 around a point estimate of 0.75. The interval is the most direct summary of precision for the reported relative comparison: it shows that the estimate is not pinned down to a narrow range. It includes 1, the value corresponding to equal hazards, as well as values on either side of 1. Thus the posted estimate is compatible with a range of relative effects, including no difference and effects favoring either dose group under the stated comparison direction.

The p value of 0.078 is consistent with uncertainty in the primary comparison, but the p value should not be used as a substitute for the interval. A p value does not state the probability that the observed effect is real, and it does not quantify the size of the effect. Likewise, the point estimate alone does not describe how precisely the effect was estimated.

The median progression-free survival estimates are 8 months and 4 months. Their interquartile ranges are 2.8 to 16.6 months and 2.7 to 11.1 months. These ranges describe the spread of the event-time distributions, not confidence intervals around the medians. The endpoint record identifies the dispersion as an interquartile range, so those bounds should not be interpreted as a 95% confidence interval.

For the secondary outcomes, the reported 95% confidence interval for the objective-response odds ratio is 0.93 to 2.24, and the reported 95% confidence interval for the clinical-benefit odds ratio is 1.04 to 1.80. The first includes 1 and the second does not. These estimates concern different outcomes from the primary endpoint and are secondary analyses. Their intervals provide information about their own precision, but they do not resolve uncertainty in the primary progression-free survival comparison.

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 sample-size figures are planning illustrations based on the observed effects, not the original design justification. The registry record does not report the trial’s original sample-size assumptions. For the primary time-to-event comparison, the figures are total event counts, not participants per arm. For the other outcomes, the figures are participants per arm.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld method and report total events; the other illustrations report participants per arm. These are planning assumptions for the illustrations and should not be mistaken for the trial’s own design assumptions.

For the primary endpoint, planning for 100% of the observed effect gives 380 total events for 80% power and 508 for 90% power. Planning for 75% of the observed effect gives 675 and 903 total events, respectively. Planning for 50% of the observed effect gives 1,518 and 2,032 total events, respectively.

For a binary outcome, the 80% power column means the illustrated number of participants per arm under the stated assumptions that would give an 80% chance of detecting the chosen effect if that effect were present. The 90% column represents a higher target chance under the same assumptions and therefore requires more participants. The illustrations show the same general pattern across outcomes: smaller effects require more participants to detect. For example, the objective-response illustration at 100% of the observed effect is 209 participants per arm for 80% power, while the 50% illustration is 910 per arm; the corresponding clinical-benefit figures are 167 and 685 per arm.

These calculations are not observed power. They are planning illustrations anchored to the observed effect estimates, and the estimates themselves are uncertain. They do not show that the completed trial had a particular probability of detecting an effect after its results were known.

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 = 0.750, so ln(HR) = -0.2877.
2. d = 4 × (1.96 + 0.842)² / [ln(0.750)]² = 379.4, rounded up to 380 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 <- 0.75                              # 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(1300351)
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 = 380 (80% power), 508 (90% power)
 75% of observed effect: events = 675 (80% power), 903 (90% power)
 50% of observed effect: events = 1,518 (80% power), 2,032 (90% power)
Simulated power with 380 events: 0.791 (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 549 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 249 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 <- 4          # control-arm median, months (converted from the posted unit)
hr          <- 0.75          # 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: 310         p (1-sided)   0.0001
 Events: 172        ~HR at bound   0.5671
   Month: 14    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.75   0.0338
   IA 2: 67%                   Z   2.5114
      N: 506         p (1-sided)   0.0060
 Events: 343        ~HR at bound   0.7622
   Month: 22    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.75   0.5603
       Final                   Z   1.9930
      N: 550         p (1-sided)   0.0231
 Events: 514        ~HR at bound   0.8387
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.75   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

For progression-free survival, the registry reports the sponsor’s primary analysis as a stratified log-rank comparison, with a hazard ratio of 0.75, a 95% confidence interval of 0.54 to 1.03, and p = 0.078. The recalculation framework for time-to-event outcomes uses only the sponsor’s reported hazard ratios; it does not replace that analysis with a new estimate. The registry record specifies stratification by last endocrine therapy before fulvestrant, AO versus AI.

For the secondary binary outcomes, the sponsor reports logistic-regression odds ratios. For objective response, the reported odds ratio is 1.44, with a 95% confidence interval of 0.93 to 2.24 and p = 0.107. For clinical benefit, the reported odds ratio is 1.37, with a 95% confidence interval of 1.04 to 1.80 and p = 0.023. The simple unadjusted recalculations use posted summary counts and a different estimand, such as a risk difference, rather than reproducing the sponsor’s logistic-regression model.

Those distinctions matter: a model-based odds ratio and an unadjusted difference in outcome proportions are not interchangeable measures. They may also yield different p values because the estimands and methods differ. When describing the trial’s own inferential results, the sponsor’s reported analysis takes precedence over a simple recalculation. Recalculated summaries can be useful as an additional descriptive check, but they should be labeled as unadjusted and should not be presented as the sponsor’s analysis.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies progression-free survival as the primary outcome and lists objective response rate, clinical benefit rate, duration of response, and duration of clinical benefit as secondary outcomes. It reports numerical analyses for the primary endpoint and for two secondary outcomes. The record does not report a plan for controlling multiplicity across secondary endpoints or across any additional analyses. It is therefore not possible to determine from the registry record whether the secondary tests were adjusted, ordered in a prespecified sequence, or intended as exploratory.

Multiplicity matters because repeated testing can increase the chance of obtaining at least one result that appears statistically notable even when the underlying effects are absent. A nominal p value for a secondary endpoint should consequently be interpreted with the number and role of the analyses in mind. The reported clinical-benefit p value is part of that broader set of outcomes; its interpretation is not identical to the primary endpoint’s interpretation.

The primary analysis description specifies a log-rank test stratified by last endocrine therapy before fulvestrant, AO versus AI. The registry record does not report whether interim analyses were planned or conducted, or whether any statistical monitoring or adjustment rules were used. It also does not report the original sample-size justification. Those details cannot be inferred from the observed endpoint estimates or from planning illustrations based on the observed effect.

The primary population is described as the FAS: all randomized patients analyzed according to randomized treatment, regardless of treatment actually received. This gives a clear stated basis for assignment to the primary analysis groups. The registry record does not provide further details about missing endpoint data, censoring patterns, reasons for loss to follow-up, or sensitivity analyses addressing missing data. The progression-free survival definition includes death as an event when it occurs in the absence of progression, but that definition does not establish how other incomplete follow-up was handled.

The record lists four secondary outcomes but only two with quantitative results in the registry record for this analysis. Missing numerical results should not be interpreted as zero events or as evidence that an outcome was not measured. The status of those results is not reported in the registry record.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyrexia (1.8%), arthritis bacterial (1.8%), hepatic function abnormal (0.9%), haemoglobin decreased (0.9%), bone pain (0.9%).

The registry reports serious adverse events in 4 participants among 109 at risk in the fulvestrant 500 mg group and 9 among 110 at risk in the fulvestrant 250 mg group. Other adverse events are reported for 68 among 109 at risk and 65 among 110 at risk, respectively. These are separate registry categories: the serious-event counts should not be added to the other-event counts, and the record does not establish whether categories overlap.

The registry lists pyrexia and bacterial arthritis at 1.8% each among the top serious-event terms, and hepatic function abnormal, decreased haemoglobin, bone pain, and cerebral infarction at 0.9% each. These listed percentages describe the reported terms; they do not establish that the same participants experienced multiple terms or identify an arm-specific rate for each term. Death counts are not reported in the registry record.

These figures are descriptive safety counts, not a formal comparison adjusted for exposure time, baseline risk, or other factors. The record does not supply event timing, duration, severity grades beyond the serious-event classification, or detailed attribution to treatment. The counts should therefore be read as the recorded adverse-event information, not as a complete assessment of comparative safety.

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

The primary result describes the comparison of progression-free survival between randomized fulvestrant dose groups in the trial population. The estimated hazard ratio is below 1 for 500 mg relative to 250 mg, but its 95% confidence interval extends from 0.54 to 1.03 and includes 1. The p value is 0.078. Taken together, these figures indicate uncertainty about the size and direction of the relative hazard difference. They do not establish that the two groups had identical outcomes, nor do they establish a definitive difference.

The reported medians, 8 months and 4 months, are useful descriptive summaries but are not the whole time-to-event result. The distribution of event times and the statistical uncertainty around the relative comparison also matter. The interquartile ranges are 2.8 to 16.6 months and 2.7 to 11.1 months, respectively. These summaries cannot predict an individual participant’s course.

The secondary outcomes describe other aspects of recorded response. The sponsor’s reported analysis for clinical benefit differs in statistical pattern from its objective-response analysis, and both are secondary to the primary endpoint. The registry record does not report a multiplicity plan, so the secondary p values should not be treated as independent confirmation of the primary result. Nor do secondary outcomes supply missing quantitative results for duration of response or duration of clinical benefit.

The findings apply to the population and analysis described: postmenopausal women with ER+ advanced breast cancer after previous endocrine therapy, with the brief summary specifying Chinese women. The primary analysis used the FAS and assigned participants according to randomized treatment. The results do not automatically generalize to other populations, disease settings, regimens, or follow-up conditions.

These statistics are not medical advice and do not determine which regimen is appropriate for an individual. They describe the registry-reported trial estimates and their precision. Clinical decisions require broader evidence and individual clinical context, neither of which is evaluated by these trial statistics alone.

19. Why This Trial Matters Statistically

This trial illustrates why a time-to-event result should not be reduced to a comparison of medians. The reported medians are 8 months and 4 months, while the primary inferential comparison is a hazard ratio of 0.75 with a 95% confidence interval of 0.54 to 1.03. The medians summarize the center of each event-time distribution; the hazard ratio compares relative event rates over follow-up. Each answers a different statistical question.

It also shows why estimates and uncertainty need to be read together. The point estimate lies below 1, but the confidence interval includes 1 and extends across a range of relative values. The p value of 0.078 adds information about the primary test under its assumptions, but it does not measure clinical importance or establish the probability that a hypothesis is true. A reader who focuses only on the point estimate or only on a threshold for the p value would miss important uncertainty.

The design and analysis descriptions also matter. Randomization, double blinding, and a parallel-group structure describe how the comparison was organized; the stated stratification identifies one factor accounted for in the primary log-rank test. The FAS definition makes clear that the primary analysis follows randomized assignment regardless of treatment received. These features help explain what the reported comparison represents, while leaving other protocol and analysis details unreported.

Finally, the secondary findings and planning illustrations demonstrate two recurring interpretation issues. Several outcomes create multiplicity questions, and planning requirements based on observed effects are not evidence of observed power. Separating primary from secondary results, sponsor analyses from simple recalculations, and estimates from planning assumptions makes the statistical evidence easier to interpret without overstating what the registry record establishes.

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 report the original sample-size justification, detailed missing-data procedures, censoring patterns, or whether interim analyses were planned or conducted. It also does not report a multiplicity strategy for the secondary outcomes. These omissions limit assessment of how the analysis plan governed the range of outcomes and tests.

The primary endpoint is reported with medians, interquartile ranges, and a hazard ratio, but the record does not provide further detail about the estimated event-time curves or the number of progression or death events. The endpoint arm counts are 111 and 110, while the overall enrollment entry is 249; the registry record does not explain the difference. The reason for any difference between enrollment and the endpoint counts is therefore not established.

The record lists four secondary outcomes but contains quantitative results for only objective response and clinical benefit in the available outcome details. Results for duration of response and duration of clinical benefit are not reported in the registry record. The safety information is also limited: serious and other adverse-event counts are available, but event timing, exposure-adjusted rates, treatment attribution, and death counts are not reported in the registry record.

The brief summary identifies Chinese postmenopausal women, and the official title identifies postmenopausal women with ER+ advanced breast cancer progressing or relapsing after previous endocrine therapy. The findings should be interpreted within that stated setting rather than assumed to apply to populations not described. The record gives the primary analysis method and stratification factor, but it does not provide enough information to reconstruct every modeling or operational decision.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Comparing the Efficacy and Tolerability of Fulvestrant 500 mg Versus 250 mg in Advanced Breast Cancer Women — NCT01300351.
• Registry record last updated 2015-04-24; status last verified 2015-04.
• Results first posted 2015-04-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

The registry describes a completed phase 3, randomized, double-blind, parallel-group, multicentre comparison of fulvestrant 500 mg and 250 mg in postmenopausal women with ER+ advanced breast cancer after previous endocrine therapy. Enrollment is listed as 249. The primary outcome is progression-free survival over 36 months, analyzed in the FAS using a log-rank test stratified by last endocrine therapy before fulvestrant.

The reported primary hazard ratio is 0.75, with a 95% confidence interval of 0.54 to 1.03 and p = 0.078. The record also reports objective response and clinical benefit analyses, and lists additional secondary outcomes without quantitative results in the available outcome details. Safety counts are descriptive, and the registry record does not report the original sample-size justification, a multiplicity plan, or detailed missing-data procedures.