Docetaxel in Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Docetaxel in Breast Cancer (NCT00312208), a randomized phase 3 study. The primary outcome is Local, Regional or Metastatic Relapse, or Second Primary Cancer, or Death From Any Cause (Disease-Free Survival).

2. Clinical Question

The registry describes a multicenter, randomized comparison of the two regimens as adjuvant treatment. In plain terms, the clinical question concerns whether the sequence of chemotherapy drugs was associated with a difference in the time until a defined disease-free-survival event. The event definition combines cancer recurrence, a second primary cancer, and death, so it captures more than recurrence alone.

The registry also lists toxicity and quality of life as secondary objectives, and says that pathologic and molecular markers were to be evaluated for predicting efficacy. The posted outcome information includes overall survival as a secondary endpoint. A trial result can address the comparison between assigned treatment strategies in the studied population, but it does not by itself establish how the regimens compare for every patient group or for outcomes not reported in the registry record.

3. Trial Design

This was a randomized, parallel-group, phase III trial with no masking listed in the registry record. The trial compared AC followed by docetaxel with docetaxel combined with doxorubicin and cyclophosphamide (TAC). The listed enrollment was 3299. The record identifies Sanofi as the sponsor and gives a start of 2001-11 and primary completion of 2008-10; the study status is completed.

The registered population was patients with operable breast cancer, HER2neu-negative disease, and positive axillary lymph nodes. The registry describes the primary efficacy analysis as using the intent-to-treat population. That approach generally analyzes participants according to their randomized assignment, regardless of whether they completed the assigned treatment; this is a general explanation of the term, not a claim about unreported details of trial conduct.

The two reported groups each have a listed arm size of 1649 for the primary outcome. The outcome record describes a median follow-up of 65 months. The primary outcome was initially intended to be expressed as median disease-free-survival time, but the registry says the median time-to-event was not reached in either group. It therefore presents the number of participants with an event by the end of the study period.

The registry lists overall survival as a secondary outcome, with a median follow-up of 65 months. It also lists two outcome measures and two analyses, while one secondary outcome is posted. The detailed original protocol, the rationale for the planned enrollment, the trial's prespecified statistical plan, interim-analysis procedures, and the masking rationale are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary efficacy analysis was performed on the Intent-to-Treat (ITT) population. Although the original Outcome Measure was intended to be presented as median disease free survival time, median time-to-event was not reached in any group; therefore, number of participants with relapse was presented.

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.

6. Primary Endpoint

The registry lists the primary outcome as Local, Regional or Metastatic Relapse, or Second Primary Cancer, or Death From Any Cause (Disease-Free Survival), measured over Median follow-up 65 months.

The primary endpoint combines the first occurrence of local, regional or metastatic relapse, a second primary cancer, or death from any cause. The registry defines the primary event as whichever of these occurs first and describes the primary efficacy analysis as measuring time from randomization to that event. This time-to-event definition preserves information about when an event occurred, rather than treating all events as if they happened at the same point in follow-up.

The registry originally intended to report median disease-free-survival time. It states that the median was not reached in either group, so the posted measured values instead give the numbers of participants with an event at the end of the study period. The primary outcome record gives median follow-up of 65 months. These event counts are a compact way to describe how many participants experienced the composite endpoint during the available observation, but they do not show when each event occurred or how follow-up varied across participants.

Using a composite endpoint can capture several clinically important outcomes in one measure and can make a time-to-event comparison possible when no group reaches the median event time. Its interpretation depends on the included events: a difference in the composite could reflect differences in any of its components. Component-specific results are not reported in the registry record, so the composite count alone cannot identify which event types contributed most to the observed pattern.

7. Results Posted in the Registry

• Docetaxel + Doxorubicin and Cyclophosphamide (TAC): 21.3% (352/1649) versus 21.6% (356/1649) on control; risk difference -0.2 percentage points (95% CI -3.0 to 2.6), risk ratio 0.99 (0.87–1.13); unadjusted two-proportion z-test p = 0.865.

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.

Death From Any Cause (Overall Survival)

• 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:
  • Docetaxel + Doxorubicin and Cyclophosphamide (TAC): 12.2% (202/1649) versus 11.3% (187/1649) on control; risk difference 0.9 percentage points (95% CI -1.3 to 3.1), risk ratio 1.08 (0.90–1.30); unadjusted two-proportion z-test p = 0.418.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Docetaxel + Doxorubicin and Cyclophosphamide (TAC) and the control. The interval gives the range of effects that remain compatible with the data.

Overall survival is the posted secondary endpoint. Its time-to-event analysis and the unadjusted comparison based on event counts both have confidence intervals that include no difference. The point estimates across the primary and secondary outcomes do not all point in the same direction: the primary risk-difference estimate and the overall-survival risk-difference estimate have opposite signs. This variation is a reminder that related outcomes need not produce identical estimates, particularly when one outcome is a composite and another concerns death from any cause.

The overall-survival analysis is related to, but distinct from, disease-free survival. Death is part of the primary composite endpoint, while overall survival counts death from any cause as its outcome. A participant can have a disease-free-survival event through relapse or a second primary cancer without having died. Thus, the secondary result is not simply a repeat of the primary endpoint, and it does not resolve which components drive the primary pattern.

The registry lists toxicity and quality of life among the secondary objectives and describes an objective to evaluate pathologic and molecular markers. However, the posted secondary outcome information available in the record is limited; conclusions about those objectives are not reported in the registry record. The posted outcome list identifies overall survival, and further endpoint-specific results should not be inferred from the study objectives alone.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis because secondary comparisons may be numerous, exploratory, or not protected against the increased chance of chance findings from repeated testing. This is a general statistical concern, not a statement that a particular adjustment was or was not performed in the trial's underlying protocol. Multiplicity procedures are not reported in the registry record. The secondary findings are best considered alongside the primary endpoint and the full uncertainty intervals, rather than as independent confirmation of a treatment difference.

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

• Death From Any Cause (Overall Survival)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results combine analyses that answer related but not identical questions. The primary outcome is defined as time from randomization to the first qualifying disease-free-survival event. The registry reports a log-rank analysis summarized as a hazard ratio, while the recalculated comparison uses the event counts in each group to estimate an unadjusted risk difference. Overall survival is also reported with a log-rank hazard ratio and an unadjusted risk difference based on counts. Differences between these measures are expected because they use different aspects of the data.

What does the risk difference describe?

As a general statistical explanation, a risk difference subtracts the event proportion in one group from the event proportion in the comparison group. It is expressed on the absolute proportion scale. A value of zero corresponds to equal observed proportions; a negative or positive value indicates which group has the lower or higher observed proportion under the comparison's stated ordering. The recalculated risk differences are unadjusted summaries of the posted counts. They do not account for event timing, and they should not be read as adjusted causal estimates beyond the randomized comparison represented by the data.

What does a hazard ratio describe?

As a general explanation, a hazard ratio compares the instantaneous event rates between groups over follow-up, conditional on remaining event-free up to a given time. It uses event timing and censoring information rather than only the final count of participants with an event. A value near one indicates similar estimated event rates under the analysis; values below or above one indicate a lower or higher estimated rate in the numerator group according to the analysis's group ordering. A hazard ratio is not a risk ratio and cannot be interpreted directly as a percentage-point difference in event probability.

The log-rank method is a standard method for comparing time-to-event patterns between groups. It evaluates whether observed event timing differs from what would be expected if the groups had similar event-time distributions. The registry reports the method and hazard ratio for the primary and secondary time-to-event analyses, but it does not report further model details or assumptions in the record. In general, interpretation of a hazard ratio is most straightforward when the relative event rates are reasonably stable over time; whether that condition was checked is not reported in the registry record.

Why can the interval include values on both sides of no difference?

A confidence interval describes the range of estimates reasonably compatible with the observed data under the method used. As a general explanation, an interval that includes the null value does not provide a clear distinction from no difference at the stated confidence level. It also does not prove that the true effect is exactly zero. The risk-difference intervals for both outcomes span zero, and the reported hazard-ratio intervals span one, the corresponding null value for a ratio.

The p-values are another summary of compatibility between the data and a specified null model, under the assumptions of the method. A large p-value is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. For these outcomes, the reported p-values do not indicate strong evidence against no difference. They should be interpreted alongside the estimates and confidence intervals rather than as a stand-alone decision rule.

Why do over-dispersion and outcome definition matter?

As a general statistical note, over-dispersion occurs when observed variability is greater than a model expects. It can make standard errors too small if ignored, which can lead to confidence intervals that are too narrow and tests that appear more decisive than warranted. The reported primary endpoint is a time-to-event outcome, and the registry does not provide information about an over-dispersion assessment. Over-dispersion is more directly relevant to certain count models and is not a claim about this trial's analysis.

The primary endpoint is composite. A composite can improve event capture by including multiple types of outcome, but a single summary can obscure whether its components move in the same direction or differ in importance. The registry record defines the components but does not post component-specific results. It also says median disease-free-survival time was not reached in either group, which explains why participant event counts are presented as measured values instead of median times. Counts alone discard the timing information used in the log-rank analysis.

The reported primary efficacy population is intent-to-treat. The record does not describe missing-data procedures, censoring rules in detail, adjustments for baseline covariates, or sensitivity analyses. Those omissions limit how specifically the posted estimates can be audited from the registry record alone. The recalculated comparisons are simple unadjusted re-calculations from the posted summary statistics; the sponsor's reported log-rank results remain the registry's own time-to-event analyses.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate less statistical uncertainty under the analysis, while wider intervals leave a broader range of effect sizes compatible with the data. The primary risk-difference estimate is -0.002, with a 95% confidence interval from -0.030 to 0.026. This interval includes zero, so the event-count comparison is compatible with no absolute difference as well as with negative or positive differences within the stated bounds.

The corresponding reported hazard ratio is 1.00, with a 95% confidence interval from 0.86 to 1.16. That interval includes one, the null value for a ratio, and allows for a range of relative event-rate differences. The risk-difference and hazard-ratio intervals should not be compared as though they measured the same quantity: one is an absolute comparison of event proportions and the other summarizes relative rates over follow-up.

For overall survival, the unadjusted risk difference is 0.009, with a 95% confidence interval from -0.013 to 0.031. The reported hazard ratio is 0.91, with a 95% confidence interval from 0.75 to 1.11. Both intervals include their respective null values. The intervals therefore do not establish a precise direction of difference, even though the point estimates themselves have directions.

Confidence intervals are not guarantees that the true effect lies inside the interval. As a general explanation, they describe the long-run behavior of the interval-producing method under its assumptions. Their practical value is to show that the posted estimates carry uncertainty and that the data are compatible with more than one possible effect. They do not, by themselves, determine whether any possible effect would be clinically important. The registry does not report a threshold for clinical importance or an equivalence margin.

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 calculations are planning illustrations based on the observed effects, not a reconstruction of the trial's original design. For the participant-count outcomes, the figures are participants per arm. In general, time-to-event planning entries based on the stated Schoenfeld approach refer to total events, but these posted outcomes are participant counts and their figures are per arm.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect: 100%, 75%, or 50%. The 80% power column gives the number of participants per arm in the planning illustration for an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column uses the same interpretation with a higher target chance of detection. Neither column describes the probability that the observed result is correct.

The figures increase as the effect to be detected becomes smaller. That is a general feature of statistical planning: a subtler difference is harder to distinguish from random variation, so more participants are needed under otherwise similar assumptions. The very large figures associated with the small observed risk differences reflect the difficulty of planning around effects of that size using the stated approach; they are not enrollment recommendations for a future study.

The trial's original sample-size justification and design assumptions are not reported in the registry record. These figures are planning illustrations calculated from observed effects, not observed power. Observed power is not a useful substitute for interpreting the estimates and their confidence intervals after a trial has been completed.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.216; treatment proportion p₁ = 0.213; average p̄ = 0.215.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5807 = 1.1381.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5807 = 0.4887.
4. n = (1.1381 + 0.4887)² / (-0.0024)² = 449,769.1, rounded up to 449,770 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.215888417222559                          # control proportion
p1 <- 0.213462704669497                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

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

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(312208)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 449,770 (80% power), 602,113 (90% power)
 75% of observed effect: n per arm = 800,411 (80% power), 1,071,523 (90% power)
 50% of observed effect: n per arm = 1,802,769 (80% power), 2,413,396 (90% power)
power.prop.test: 449769.1 
Simulated power at n = 449,770 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's reported analysis of the primary outcome is a log-rank time-to-event comparison. It gives a hazard ratio of 1.00, a 95% confidence interval from 0.86 to 1.16, and p = 0.978. The recalculated comparison uses the posted participant event counts to estimate an unadjusted risk difference of -0.002, with a 95% confidence interval from -0.030 to 0.026 and an unadjusted p-value of 0.865.

These results are not duplicate calculations of exactly the same quantity. The sponsor's reported analysis incorporates event timing, whereas the re-calculation summarizes the proportions with an event in the posted counts and does not use timing. The estimates and p-values can therefore differ without implying an error. Both analyses are consistent with little separation in the posted data, and both confidence intervals include their respective null values.

The registry does not flag a discrepancy between the posted summary information and the re-calculation. The reported log-rank analysis should be understood as the trial's own time-to-event result, while the unadjusted calculation is a supplementary summary of the posted counts. Neither should be mistaken for an analysis adjusted for unreported covariates or for proof of equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies disease-free survival as the primary objective and overall survival as a secondary outcome. It also names toxicity, quality of life, and evaluation of pathologic and molecular markers among the objectives. The posted record does not describe a multiplicity adjustment or explain how statistical interpretation was to account for testing multiple outcomes, time points, or markers. A prespecified statistical analysis plan is not reported in the registry record.

As a general statistical explanation, the more hypotheses examined, the greater the chance that at least one result will appear unusual by chance alone if each is assessed separately. Methods for controlling multiplicity can limit that problem, but no particular method should be assumed for this trial from the information in the registry. Consequently, secondary comparisons are appropriately interpreted as less definitive than a clearly prespecified primary analysis, especially when the number of planned comparisons and adjustment strategy are not described.

The registry states that the primary efficacy analysis used the intent-to-treat population. It does not provide comparable population details for every outcome in the posted record. The method for handling missing outcome information, the extent of missingness, and any sensitivity analyses for missing data are not reported in the registry record. These details matter because missing follow-up can affect estimates, particularly for time-to-event outcomes when censoring and loss to follow-up are involved.

The registry describes the primary endpoint as time from randomization to the first qualifying event and presents event counts because the median time-to-event was not reached in either group. More detailed censoring rules, protocol deviations, and the handling of participants without complete follow-up are not reported. Interim-analysis plans, stopping rules, and any related adjustment to the statistical threshold are also not reported in the registry record. These gaps limit a full assessment of the analysis process, but they do not alter the numerical results that are posted.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fever (including serious febrile neutropenia) (17.9%), infection (including neutropenic infection) (8.7%), leukopenia (3.4%), vomiting (1.7%), nausea (1.2%).

The registry lists serious adverse events for both treatment groups. The count recorded as affected is 331 among 1634 at risk in the AC → T group and 520 among 1635 at risk in the TAC group. These are serious-adverse-event figures, not counts of disease-free-survival events, and should be read separately from the efficacy outcomes. The registry does not provide a comparative statistical analysis of these safety counts in the posted information.

The listed serious adverse-event terms include fever, including serious febrile neutropenia, at 17.9%; infection, including neutropenic infection, at 8.7%; leukopenia at 3.4%; vomiting at 1.7%; nausea at 1.2%; and deep thrombophlebitis at 0.9%. These are the terms and percentages listed in the registry record. The record does not give enough detail to establish whether events could be counted under more than one term or to describe their timing and duration.

Serious adverse-event counts alone do not summarize every aspect of tolerability. The registry record does not report a complete adverse-event profile in the information described, nor does it give a safety comparison adjusted for exposure or follow-up. The figures should therefore be treated as descriptive registry results rather than as a stand-alone estimate of the relative safety of the regimens.

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

The posted primary results show similar observed disease-free-survival event counts in the two randomized groups, and the estimated difference is small on the absolute scale. The confidence intervals for the unadjusted risk difference and the reported hazard ratio include their respective null values. The registry's log-rank analysis likewise does not show a clear statistical separation between the treatment sequences. These results describe the data available in the record; they do not establish that the strategies are identical.

A non-significant result is not proof of no effect. It may reflect a genuinely small difference, uncertainty around the estimate, or both. The intervals allow a range of possible effects, and the registry record does not report a prespecified equivalence or non-inferiority margin. It is therefore not appropriate to interpret the findings as demonstrating equivalence or as ruling out every meaningful difference.

The endpoint is a composite of relapse, second primary cancer, and death. Because component-specific results are not reported in the registry record, the combined outcome cannot identify which events contributed to the observed counts. The counts also do not convey event timing, although the reported log-rank analysis does use time-to-event information. Median disease-free-survival time was not reached in either group, so the registry presents participant event counts instead of median times.

Overall survival is a secondary outcome and has uncertainty that also includes no difference. Its pattern should be considered alongside, but not substituted for, the primary endpoint. The record also includes serious adverse-event summaries, but those descriptive figures do not alone provide a complete comparison of benefit and harm. Finally, these findings apply to the population and treatment strategies described in the record; they do not automatically generalize to other disease groups, treatment settings, or outcomes not posted.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question about treatment sequence: whether giving docetaxel with doxorubicin and cyclophosphamide differs in disease-free survival from giving doxorubicin and cyclophosphamide followed by docetaxel. Its randomized parallel-group design makes the comparison between assigned strategies central to interpretation, while the registry's intent-to-treat description indicates that the primary efficacy analysis was based on randomized assignment.

The record also illustrates why endpoint definitions matter. Disease-free survival is not recurrence alone; it combines relapse, a second primary cancer, and death. The registry reports that the planned median time-to-event was not reached in either group and therefore presents event counts, while also reporting a log-rank hazard ratio that uses time-to-event information. Those approaches offer related but different views of the data. Reading the estimates with their confidence intervals helps prevent a p-value from becoming the only basis for interpretation.

Another important statistical lesson is the distinction between a lack of clear evidence for a difference and evidence that differences are absent. Both the primary and secondary estimates have uncertainty, and no equivalence margin is reported. The planning illustrations also show, in general, that sample-size requirements grow when the effect targeted for detection is smaller. They should be understood as planning calculations rather than retrospective proof about the study's power.

Finally, the registry record makes visible the limits of what can be concluded from posted results. It identifies the primary analysis population and reports outcome estimates, but detailed multiplicity procedures, missing-data methods, and original design assumptions are not reported. This case therefore provides a practical example of interpreting randomized-trial results while keeping the estimand, analysis method, precision, and reporting gaps distinct.

19. 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 the original sample-size justification, the assumptions used to design the trial, or a detailed statistical analysis plan. The planning figures associated with the posted results are illustrations calculated from observed effects and should not be treated as the original design rationale. The record also does not report a prespecified equivalence or non-inferiority margin, limiting any claim that the regimens were equivalent.

There is limited detail about missing data and follow-up. The primary outcome record gives median follow-up of 65 months and says the median disease-free-survival time was not reached in either group, but detailed censoring rules, the amount of missing outcome information, and sensitivity analyses are not reported in the registry record. Those details would help assess how incomplete follow-up may affect time-to-event estimates.

The primary endpoint combines several different event types, while component-specific results are not reported. The registry also does not report the detailed analysis population for every endpoint or explain whether estimates were adjusted for baseline characteristics. Multiplicity procedures for the secondary objectives and any interim-analysis plan are not reported in the registry record. Therefore, the secondary outcomes and exploratory objectives cannot be assessed against a fully described testing strategy.

The safety information is also limited to the serious adverse-event figures and selected terms described in the record. A fuller account of event definitions, timing, exposure, and the handling of overlapping events is not reported. These limitations do not invalidate the posted estimates, but they restrict the depth of independent assessment possible from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Docetaxel in Breast Cancer — NCT00312208.
• Registry record last updated 2013-12-30; status last verified 2013-12.
• Results first posted 2010-02-17.
• 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.

23. Record Summary

The registry describes a completed, randomized, parallel-group phase III trial of adjuvant chemotherapy in operable HER2neu-negative breast cancer with positive axillary lymph nodes. It compared doxorubicin and cyclophosphamide followed by docetaxel with docetaxel combined with doxorubicin and cyclophosphamide. The primary endpoint was disease-free survival, defined by relapse, second primary cancer, or death from any cause.

The posted primary event-count comparison and the reported log-rank analysis do not show a clear difference between the groups; their confidence intervals include the respective null values. Overall survival is posted as a secondary endpoint and likewise has uncertainty spanning no difference. The registry reports serious adverse-event counts and selected event terms. Important details, including the original sample-size rationale, multiplicity procedures, and missing-data methods, are not reported in the registry record.