Palbociclib (PD-0332991) Combined With Fulvestrant In Hormone Receptor+ HER2-Negative Metastatic Breast Cancer After Endocrine Failure (PALOMA-3): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Palbociclib (PD-0332991) Combined With Fulvestrant In Hormone Receptor+ HER2-Negative Metastatic Breast Cancer After Endocrine Failure (PALOMA-3) (NCT01942135), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) as Assessed by the Investigator.

2. Clinical Question

The primary objective was to assess superiority for progression-free survival. The posted primary result is a comparison of time-to-event outcomes, not simply a count of participants who had progressed by a single date. Follow-up for the primary endpoint was assessed up to 12 months. The trial also compared safety between treatment arms and recorded several secondary outcomes, including overall survival and objective response.

The clinical question is specific to participants with metastatic disease after prior endocrine therapy. It does not directly address people with other breast cancer subtypes, disease stages, or treatment histories. The registry record describes the trial population and assigned regimens, but does not report additional eligibility details in the registry record for this analysis.

3. Trial Design

PALOMA-3 was a Phase 3, randomized, triple-masked, parallel-group trial. It enrolled 521 participants and is recorded as completed. The registry lists Pfizer as the sponsor. The start date was 2013-09-26, and primary completion was 2014-12-05. These dates describe the registry record and do not by themselves indicate the duration of follow-up for every participant.

Participants were assigned to palbociclib plus fulvestrant or placebo plus fulvestrant. The official title describes the study as multicenter, randomized, double-blind, and placebo-controlled; the registry masking field is triple. The two arm descriptions state that assigned treatment continued until objective progression, symptomatic deterioration, unacceptable toxicity, death, or withdrawal of consent, whichever occurred first. The registry record does not report treatment doses in the registry record.

The primary endpoint was investigator-assessed progression-free survival in the intent-to-treat population. Its stated timeframe was from randomization to the first documentation of progression or death, assessed up to 12 months. Secondary outcome listings include overall survival, objective response, duration of response, clinical benefit response, and plasma trough concentrations. The registry lists 20 outcome measures and 30 analyses; 19 secondary outcomes are posted.

Randomization supports a comparison of assigned treatment groups, while masking is intended to reduce the influence of knowledge of assignment on care and assessment. These design features do not remove uncertainty from the estimates or resolve questions that were not reported, such as the original sample-size justification, interim-analysis plan, or details of the 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: The study consisted of a screening visit within 28 days before randomization, an active treatment phase, divided in cycles of 28 days each, and a post-treatment follow-up period during which survival and new anti-cancer therapy information was collected every 3 months for the first 9 months, then every 6 months from the last dose of study intervention.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent-to-treat (ITT) population or full analysis set included all participants who were randomized, with study intervention, regardless of whether participants received the study intervention or received a different drug from that to which they were randomized.

5. Baseline Characteristics

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

Population: The intent-to-treat (ITT) population or full analysis set included all participants who were randomized, with study intervention assignment designated according to initial randomization, regardless of whether participants received study intervention or received a different drug from that to which they were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) as Assessed by the Investigator, measured over From randomization date to date of first documentation of progression or death (assessed up to 12 months).

Progression-free survival (PFS) is the time from randomization to the first documented objective progression of disease or death from any cause in the absence of documented progression. It combines disease progression and death into a time-to-event endpoint, so participants can contribute information up to an event or, if no event is observed during their available follow-up, up to a censoring time.

The registry defines progression using RECIST v1.1. The definition includes a 20% increase in the sum of target-lesion diameters together with an absolute increase of at least 5mm, unequivocal progression of existing non-target lesions, or the appearance of new lesions. The registry also describes censoring: participants without a post-randomization tumor evaluation were censored on the randomization date with a duration of a day; participants whose progression or death was documented after a long interval without evaluable assessments were censored at the last objective assessment that did not show progression.

Time-to-event endpoints are useful when participants have different observation times and when the timing of an event matters. A median gives a central point on the estimated event-time distribution; it does not mean that every participant experienced the event at that time. The registry reports median PFS and a hazard ratio comparison. The hazard ratio uses information across event times rather than representing a direct difference between the two medians. The registry record does not report further detail about the PFS estimation procedure in the registry record.

7. Results Posted in the Registry

• Palbociclib + Fulvestrant vs Placebo + Fulvestrant: hazard ratio 0.42 (95% CI 0.32–0.56), reported p < 0.001 (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.

Overall Survival (OS)-Number of Participants Who Died

• 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:
  • Palbociclib + Fulvestrant: 57.9% (201/347) versus 62.6% (109/174) on control; risk difference -4.7 percentage points (95% CI -13.6 to 4.1), risk ratio 0.92 (0.80–1.07); unadjusted two-proportion z-test p = 0.301.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Palbociclib + Fulvestrant and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival (OS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Stratified Log Rank Test (1-sided)); it was not recalculated.
• Result:
  • Palbociclib + Fulvestrant vs Placebo + Fulvestrant: hazard ratio 0.81 (95% CI 0.64–1.03), reported p = =0.0429 (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 Palbociclib + Fulvestrant vs Placebo + Fulvestrant and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response (OR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Palbociclib + Fulvestrant: 21.0% (73/347) versus 8.6% (15/174) on control; risk difference 12.4 percentage points (95% CI 6.4 to 18.4), risk ratio 2.44 (1.44–4.13); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Palbociclib + Fulvestrant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question to survival, response, and other measures. Overall survival addresses time until death, whereas objective response records whether a response was observed during the stated treatment period. The registry also lists duration of response, clinical benefit response, survival probabilities at specified years, and plasma trough concentrations. These outcomes do not measure the same construct as investigator-assessed PFS, so they provide complementary rather than interchangeable evidence.

Across the posted results, the survival summaries are not equally precise: the overall-survival hazard-ratio interval spans 1, while the PFS hazard-ratio interval lies below 1. The response comparison is a binary outcome and uses a different analysis measure from the time-to-event endpoints. These patterns can be considered alongside the primary result, but they should not be collapsed into a single conclusion. Each endpoint has its own definition, follow-up window, event information, and uncertainty.

Secondary outcomes usually carry less confirmatory weight when many outcomes or analyses are examined without a reported multiplicity procedure. Testing multiple hypotheses increases the chance that at least one result appears unusual by chance. Whether and how the trial controlled that risk is not reported in the registry record. Consequently, nominal or unadjusted secondary p-values should be treated cautiously and should not be read as independent confirmation of the primary finding.

The registry lists 19 secondary outcomes as posted, but the registry entries do not give complete results for every listed outcome. The overall pattern can therefore be described only from the endpoints and values actually recorded. Missing secondary results should not be interpreted as null findings or as evidence that no analyses were performed.

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

• Overall Survival (OS)-Number of Participants Who Died
• Overall Survival (OS)
• Survival Probabilities at Year 1, Year 2, and Year 3
• Objective Response (OR)
• Duration of Response (DR)
• Clinical Benefit Response (CBR)
• Observed Plasma Trough Concentration (Ctrough) for Palbociclib
• Ctrough for Fulvestrant

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. For each participant, the relevant time begins at randomization and ends at documented progression or death, unless the participant is censored earlier under the registry rules. Censoring means that the event time is not observed during the participant’s available follow-up; it does not mean that the participant had no event ever. Valid time-to-event analysis depends on appropriate handling of censoring and on the assumptions of the method used. The registry description specifies some censoring rules, but does not report every modeling or diagnostic detail in the registry record.

What does the median describe?

The median event time is the point by which half of the estimated event-time distribution has experienced the event. It is a summary of the distribution, not an average duration for every participant and not a guarantee that an individual will remain event-free for that period. Median PFS was 9.2 months in the palbociclib-plus-fulvestrant group and 3.8 months in the placebo-plus-fulvestrant group. Medians alone do not summarize all the information about event timing, which is why the registry also reports a hazard ratio.

What does a hazard ratio describe?

A hazard is the instantaneous event rate among participants still at risk at a given time. A hazard ratio compares those rates between groups over time under the time-to-event analysis. The sponsor-reported PFS hazard ratio is 0.422. Values below 1 indicate a lower estimated hazard in the first-named group relative to the comparator under this convention; the ratio is not a probability, a ratio of medians, or a direct statement about how many participants avoid an event. A hazard ratio is most straightforward to interpret when the relative hazards are reasonably stable over time. Whether that assumption was assessed, and the result of any assessment, are not reported in the registry record.

Why is a stratified log-rank test used?

The reported PFS comparison uses a stratified log-rank test with a one-sided alternative. A log-rank test compares the observed and expected distribution of events over follow-up, accounting for censoring. Stratification means the comparison is organized across strata defined by trial factors, rather than ignoring those strata. The factors used for stratification are not reported in the registry record. A one-sided test assesses evidence in a prespecified direction; the registry record reports the test direction as one-sided but does not report the full rationale or analysis-plan details.

The reported PFS p-value is < 0.001. A p-value measures how incompatible the observed data are with a specified null model under the test assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The estimate and confidence interval are needed to understand the direction and precision of the comparison.

How do confidence intervals fit with the test?

A confidence interval expresses uncertainty around an estimate under the method used to construct it. For a hazard ratio, 1 is the value representing equal hazards. The PFS 95% confidence interval, 0.318 to 0.560, lies below 1. The interval does not imply that all values within it are equally plausible, and it does not account for every possible source of bias or analysis uncertainty.

For binary outcomes, a risk difference is a difference between event proportions, while an odds ratio compares odds. These measures use the same underlying event counts but have different scales and interpretations. The re-calculated objective-response risk difference and the sponsor-reported odds ratio are therefore not competing versions of the same numeric quantity. Unadjusted re-calculations use posted summary statistics and do not substitute for a sponsor analysis when one is reported.

Over-dispersion is a general statistical issue that arises when variability in data exceeds what a model assumes. It can make standard errors and confidence intervals too narrow if ignored. The primary outcome is time-to-event, and the registry record does not report an over-dispersion assessment; it would therefore be inappropriate to claim that it affected this analysis. More generally, model assumptions and analysis details matter because apparently precise estimates can still be sensitive to departures from those assumptions.

Randomization, masking, prespecified endpoints, and a suitable analysis population contribute to the credibility of a trial comparison. The registry identifies randomization, triple masking, and the intent-to-treat population for PFS. The exact randomization procedure, stratification factors, handling of protocol deviations, and full statistical analysis plan are not reported in the registry record. Those missing details limit how completely the analysis can be independently reconstructed from the posted summary.

11. Confidence Intervals and Precision

The PFS hazard ratio is 0.422, with a 95% confidence interval from 0.318 to 0.560. This interval is relatively close together on the hazard-ratio scale and remains below 1 throughout. It indicates that the estimate is not simply a single exact value: a range of relative hazard estimates is compatible with the data under the analysis method. The interval does not quantify uncertainty from every design, measurement, or modeling limitation.

The median PFS confidence limits are not equally complete in the registry record. For palbociclib plus fulvestrant, the listed median is 9.2 months and the lower confidence limit is 7.5 months; an upper limit is not reported in the registry record. For placebo plus fulvestrant, the median is 3.8 months and the 95% confidence interval is 3.5 to 5.5 months. Readers should not infer a missing bound from the other arm or from the hazard ratio.

The secondary overall-survival hazard ratio is 0.814, with a 95% confidence interval from 0.644 to 1.029. This interval extends across 1, so it includes estimates consistent with no relative hazard difference as well as estimates on either side. The reported one-sided p-value is =0.043; the p-value and interval answer related but not identical questions, and the interval provides useful information about the range and precision of the effect estimate.

Confidence intervals describe sampling uncertainty under specified statistical assumptions. They do not guarantee that the true effect lies within the particular interval, and a narrow interval does not eliminate bias or errors in measurement. Interpretation also depends on endpoint definitions, follow-up, censoring, and the analysis plan. The registry record does not report all details needed to evaluate those elements fully.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design justification. For time-to-event outcomes, the figures are total events required. For other outcomes, the figures are participants per arm. Thus, the PFS and overall-survival planning entries refer to total events, whereas the binary-outcome entries refer to participants in each arm.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record. In particular, the planning illustration should not be mistaken for the design calculation used to enroll 521 participants.

The 80% power column gives the event or per-arm participant count that the illustration estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column gives the corresponding count for a 90% chance. These are hypothetical design targets, not measures of how likely the observed result was to occur after the trial was completed. This is not observed power.

The rows consider the full observed effect and smaller fractions of it. When the target effect is smaller, distinguishing it from chance variation generally requires more information, so the illustrated event or participant counts rise. A planning curve is a visual way to see how those requirements change as the assumed effect changes; it should be read as a relationship under the stated assumptions, not as a forecast of the trial’s actual results.

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 = 0.422, so ln(HR) = -0.8627.
2. d = 4 × (1.96 + 0.842)² / [ln(0.422)]² = 42.2, rounded up to 43 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 <- 0.422                              # 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(1942135)
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 = 43 (80% power), 57 (90% power)
 75% of observed effect: events = 75 (80% power), 101 (90% power)
 50% of observed effect: events = 169 (80% power), 226 (90% power)
Simulated power with 43 events: 0.821 (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 63 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 521 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 <- 3.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.422          # 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: 38         p (1-sided)   0.0001
 Events: 19        ~HR at bound   0.1809
  Month: 14    P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.42   0.0338
  IA 2: 67%                   Z   2.5114
      N: 62         p (1-sided)   0.0060
 Events: 38        ~HR at bound   0.4411
  Month: 23    P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.42   0.5603
      Final                   Z   1.9930
      N: 64         p (1-sided)   0.0231
 Events: 57        ~HR at bound   0.5884
  Month: 60    P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.42   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 PFS, the sponsor-reported analysis is a stratified one-sided log-rank test and reports a hazard ratio of 0.422, a 95% confidence interval from 0.318 to 0.560, and p < 0.001. These values match the primary comparison reported in the registry. The registry does not flag a discrepancy for this analysis, and the sponsor’s reported time-to-event analysis is the relevant analysis to use when describing the primary result.

Some secondary outcomes also have sponsor-reported analyses. For overall survival, the reported analysis gives a hazard ratio of 0.814 with a 95% confidence interval from 0.644 to 1.029 and a one-sided p-value of =0.043. For objective response, the sponsor reports an exact one-sided test with an odds ratio of 2.783 and a 95% confidence interval from 1.563 to 5.603. Those analyses use the sponsor’s stated methods and should be kept distinct from simple unadjusted recalculations.

Where posted summary counts permit, recalculated values can offer a transparent, unadjusted comparison. They may differ from sponsor analyses because they do not reproduce stratification, censoring, model choices, or other features of the original analysis. For objective response, the recalculated risk difference is a different effect measure from the sponsor’s odds ratio. For the death-count endpoint, no sponsor-reported analysis is listed in the registry record. Recalculations should therefore be presented as supplementary descriptions, not as replacements for a reported sponsor analysis.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study tests multiple outcomes, time points, subgroups, or analysis variants. If each test is treated as a separate opportunity to declare a finding, the overall chance of at least one false-positive result can increase. Trials may address this through a prespecified testing hierarchy, adjustment procedures, or by designating some analyses as exploratory. The registry record does not report a multiplicity adjustment or a hierarchy for the primary and secondary analyses in the registry record.

The PFS endpoint is designated primary, while the registry lists multiple secondary outcomes and analyses. This distinction matters: the primary result has a clearer confirmatory role than individual secondary results, whose interpretation may be affected by the number of tests. The one-sided tests reported for the PFS and several secondary comparisons should be understood as the stated analysis approach; the registry record does not report the full rationale, prespecification details, or whether all other analyses used the same direction or testing strategy.

For PFS, the registry describes how certain participants were censored, including participants without a post-randomization tumor evaluation and participants with a long interval between assessments before progression or death. These rules influence how observed follow-up contributes to the time-to-event analysis. The handling of missing data for the secondary outcomes, the extent of missing assessments, and any sensitivity analyses are not reported in the registry record.

The primary population is described as intent-to-treat: all randomized participants were included regardless of whether they received the assigned intervention or a different drug. This preserves the randomized assignment comparison in the stated population. The registry record does not report further information about exclusions from particular outcome analyses, protocol deviations, or analysis populations used for all secondary endpoints.

Interim analyses, stopping boundaries, the complete statistical analysis plan, and the original sample-size justification are not reported in the registry record. Their absence from this record does not establish that no such procedures existed; it means they cannot be evaluated from the information recorded. These omissions constrain independent assessment of prespecification and the handling of multiple opportunities to test hypotheses.

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: pleural effusion (1.7%), pyrexia (1.4%), ascites (1.2%), pneumonia (1.2%), pathological fracture (1.2%).

The posted safety counts use different denominators from the randomized group sizes: 345 participants were at risk for serious adverse events in the palbociclib-plus-fulvestrant group and 172 in the placebo-plus-fulvestrant group. Serious adverse events affected 78 and 33 participants, respectively. Other adverse events affected 341 of 345 and 161 of 172 participants. Death counts recorded for the groups were 201 and 109. These are counts, not adjusted comparisons, and the registry record does not give a causal attribution for each event in the registry record.

The most frequently listed serious adverse-event terms include pleural effusion at 1.7%, pyrexia at 1.4%, ascites at 1.2%, pneumonia at 1.2%, pathological fracture at 1.2%, and neutropenia at 1.2%. These listed terms are not a complete safety profile. The registry record does not report all event definitions, severity details, duration, exposure-adjusted rates, or comparative statistical analyses in the registry record.

Safety counts need to be interpreted with attention to who was included in each denominator and the period of observation. They do not, by themselves, establish that an event was caused by a treatment or quantify the balance of benefits and harms. The figures are descriptive registry results, not individual predictions.

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

The primary result describes a randomized comparison of palbociclib plus fulvestrant with placebo plus fulvestrant among women with hormone receptor-positive, HER2-negative metastatic breast cancer after prior endocrine therapy. The posted PFS estimate favors the palbociclib-plus-fulvestrant assignment on the time-to-event measures reported: median PFS was 9.2 months versus 3.8 months, and the hazard ratio was 0.422 with a 95% confidence interval from 0.318 to 0.560.

Those findings describe outcomes in the trial population under the recorded endpoint definition and follow-up. They do not establish the result for every person with breast cancer or for populations and treatment settings not represented in the registry description. A group-level median or hazard ratio cannot predict an individual participant’s outcome. Nor does a p-value determine whether an observed difference is important to a patient; it addresses compatibility with a statistical null model under the test assumptions.

The primary endpoint is not overall survival. The overall-survival estimate has a different endpoint and a wider interval that includes 1. Its uncertainty should be considered alongside the reported one-sided p-value, without treating that p-value as proof of a definitive survival effect. The response result is another distinct outcome, with a different scale and analysis method. Secondary outcomes can enrich interpretation but do not replace the designated primary endpoint.

The registry record also does not resolve all questions about long-term outcomes, subgroup effects, or the relative importance of benefits and harms. Some safety information is listed, but the posted counts alone do not establish causation or provide a full comparative safety assessment. These results are statistical descriptions of a completed clinical trial, not medical advice or a recommendation for an individual treatment choice.

19. Why This Trial Matters Statistically

This trial illustrates how a randomized, masked comparison can be framed around a time-to-event primary endpoint. PFS incorporates both the timing of progression and death, while allowing participants with incomplete event observation to contribute follow-up through censoring. The distinction between the median and the hazard ratio is especially important: one describes a point in the event-time distribution, while the other compares relative event rates across follow-up under the analysis method.

The results also demonstrate why uncertainty measures belong beside point estimates. The PFS hazard-ratio confidence interval remains below 1, while the overall-survival interval extends across 1. The contrast emphasizes that related outcomes can have different precision and should not be treated as if they answer the same question. A reported p-value alone cannot convey the range of effect estimates compatible with the data.

The registry record makes visible another important statistical distinction: sponsor analyses and simple recalculations may use different outcome measures and methods. A recalculated risk difference for a binary endpoint is not a substitute for a sponsor-reported odds ratio or a stratified survival analysis. Clear labeling of each method helps readers understand which results are directly reported and which are supplementary unadjusted summaries.

Finally, the record includes many secondary outcomes, while not reporting a multiplicity plan in the registry record. This makes prioritizing the primary endpoint and treating secondary findings cautiously essential to a disciplined reading. The trial is therefore a useful example of how design, endpoint definition, censoring, precision, and multiplicity all shape interpretation—not merely whether a p-value falls below a threshold.

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 provides a concise outcome description, but several details needed for a fuller assessment are not reported in the registry record. The PFS median for palbociclib plus fulvestrant has a listed lower confidence limit but no upper limit. The confidence interval for the placebo-plus-fulvestrant median is reported, but the two medians should not be compared as though their separate intervals were a formal test of the between-group difference; the hazard-ratio analysis is the reported comparative time-to-event result.

The registry describes the PFS population as intent-to-treat and gives specific censoring rules, but does not report all details of the analysis implementation, such as the stratification factors, checks of time-to-event assumptions, or sensitivity analyses. The registry also does not report the original sample-size justification, interim-analysis procedures, or a multiplicity plan. These are limits on what can be independently assessed from the registry record, not evidence that those procedures were absent.

Follow-up windows differ across outcomes: the primary PFS assessment was up to 12 months, objective response was assessed up to 2 years, and overall survival was followed up to 4.5 years. Comparisons across those outcomes therefore involve different observation periods and endpoint definitions. The registry entries do not include complete results for every listed secondary outcome or full details of missing assessments.

The safety summary gives counts, denominators, and selected serious adverse-event terms, but does not provide a comprehensive account of event timing, duration, severity, exposure, or attribution. The record also does not report subgroup estimates in the registry record. These limitations counsel against extending the findings beyond the population, endpoints, and analyses actually recorded.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Palbociclib (PD-0332991) Combined With Fulvestrant In Hormone Receptor+ HER2-Negative Metastatic Breast Cancer After Endocrine Failure (PALOMA-3) — NCT01942135.
• Registry record last updated 2024-04-04; status last verified 2024-04.
• Results first posted 2016-05-23.
• 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

PALOMA-3 was a completed, randomized, triple-masked, parallel-group Phase 3 trial enrolling 521 participants. It compared palbociclib plus fulvestrant with placebo plus fulvestrant in women with hormone receptor-positive, HER2-negative metastatic breast cancer whose disease progressed after prior endocrine therapy.

The primary endpoint was investigator-assessed PFS in the intent-to-treat population. Median PFS was 9.2 months versus 3.8 months; the reported hazard ratio was 0.422, with a 95% confidence interval from 0.318 to 0.560 and p < 0.001. The registry also posts overall-survival, response, and safety outcomes, which have distinct definitions and levels of precision.

Important statistical details—including the original sample-size justification, interim-analysis procedures, and multiplicity plan—are not reported in the registry record. Secondary results should be interpreted in that context, and descriptive safety counts should not be treated as causal comparisons.