Doxorubicin HCI Liposome Injection Versus Weekly Docetaxel in Patients First Relapse Metastatic Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Doxorubicin HCI Liposome Injection Versus Weekly Docetaxel in Patients First Relapse Metastatic Breast Cancer (NCT00193037), a randomized phase 2 study. The primary outcome is Overall Response Rate (ORR), the Percentage of Patients Who Experience an Objective Benefit From Treatment.

2. Clinical Question

The registry’s stated aim was to evaluate single-agent liposomal doxorubicin against single-agent docetaxel as first-line treatment in metastatic breast cancer, with crossover to the opposite treatment after progression or intolerance. It also states that possible cross-resistance was to be explored. However, the posted primary endpoint is overall response rate, and the available response summaries are organized by randomized sequence. A separate numerical result for cross-resistance is not reported in the registry record.

The clinical question therefore has two levels: the proportion with an objective response in each sequence group, and the contrast between those proportions. Because treatment can change after progression or intolerance, the sequence comparison should not automatically be read as a pure comparison of responses to the first assigned drug alone. Details that would establish precisely which treatment period contributed to each response estimate are not reported in the registry record.

3. Trial Design

This was a randomized, phase II, crossover study with two treatment sequences. In Arm A, participants started with liposomal doxorubicin and then crossed over to docetaxel. In Arm B, participants started with docetaxel and then crossed over to liposomal doxorubicin. The registry describes the crossover as occurring at disease progression or patient intolerance. Allocation is listed as randomized, masking as none, and the study model as crossover.

The registry lists enrollment of 102 and a completed status. The study start is recorded as 2001-02, and primary completion as 2008-12. These dates describe the registry record; they do not by themselves establish how long each participant was followed or how long treatment exposure lasted. The primary outcome timeframe is stated as 18 Months.

The arm-specific response summaries use denominators of 42 in Arm A and 44 in Arm B. The registry explicitly says that patients removed from treatment before evaluation were not included in the primary outcome analysis. The resulting response populations therefore do not include everyone enrolled. The reasons for removal, the number removed before response evaluation, and the handling of other missing outcome observations are not reported in the registry record.

The registry also lists progression-free survival as a secondary outcome, defined as the length of time in months that patients were alive from their first date of protocol treatment until worsening of their disease. A numerical PFS result is not reported in the registry record. The record identifies two outcome measures and one posted secondary outcome, but does not provide a detailed account of all planned outcomes or analyses.

In a crossover study, the order of treatment matters because participants may receive both interventions and the time of switching is linked to progression or intolerance. General statistical interpretation therefore distinguishes a comparison of randomized starting sequences from a comparison of treatment effects across all exposure periods. The registry record does not describe a period-specific analysis, a method for accounting for carryover, or a model that separates first-treatment response from later-treatment response.

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.

Randomized Treatment

Crossover Treatment

Analysis population for the primary outcome, as defined in the registry: Patients who were removed from treatment before evaluation were not included in analysis

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 Overall Response Rate (ORR), the Percentage of Patients Who Experience an Objective Benefit From Treatment, measured over 18 Months.

The primary endpoint is overall response rate, defined as the percentage of patients who exhibit a complete response or partial response. A complete response means total disappearance of clinically and radiologically detectable disease for at least 4 weeks. A partial response means at least a 50% reduction of all measurable lesions, measured by the product of the perpendicular diameters of the greatest tumor dimensions, with no new lesions for at least four weeks.

Response rate is a binary outcome at the participant level: a patient is classified according to whether an objective response was observed under the endpoint definition. The registry reports the number of responders as a percentage and gives a 95% confidence interval for each arm. The stated timeframe is 18 Months. Patients removed from treatment before evaluation were excluded from the analysis, according to the registry’s population description.

In general, an objective response endpoint is used to describe tumor shrinkage meeting prespecified criteria. It can be summarized as a proportion, which is straightforward to interpret, but it does not alone describe how long a response lasts, how symptoms change, or how long patients live without progression. Those are different outcomes. The registry lists progression-free survival as a secondary outcome, but does not report its numerical result in the record.

For this study, the endpoint is reported by randomized treatment sequence. Because the trial allowed crossover after progression or intolerance, the response rate should be interpreted with attention to the definition of the analysis population and timing of response assessment. The precise relationship between assessment timing and crossover is not reported in the registry record.

7. Results Posted in the Registry

• Arm B - Docetaxel Then Liposomal Doxorubicin: 31.8% (14/44) versus 28.6% (12/42) on control; risk difference 3.2 percentage points (95% CI -16.1 to 22.6), risk ratio 1.11 (0.58–2.12); unadjusted two-proportion z-test p = 0.743.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted response outcome is a binary proportion: the number of participants classified as having an objective response relative to the participants included in that arm’s response analysis. The endpoint combines complete and partial response under the definitions in the registry. Arm A had 12 responders among 42 analyzed participants, and Arm B had 14 among 44. The registry reports the corresponding percentages and confidence intervals.

What does a confidence interval describe?

In general, a confidence interval expresses uncertainty in an estimate arising from sampling variation. It is not a range that contains a fixed percentage of individual patient outcomes, and it does not give the probability that the true value lies inside that particular interval. Intervals are most useful when read alongside the point estimate: a wide interval signals that the data are consistent with a broad range of underlying response proportions or between-arm effects.

The arm-specific 95% confidence intervals are 16.0% to 42.0% for Arm A and 18.0% to 45.0% for Arm B. The between-sequence comparison also has a confidence interval, reported on the risk-difference scale, that crosses zero. A risk difference of zero represents no difference in the two proportions. Because the interval includes values on both sides of zero, the comparison does not rule out either direction of difference at the stated interval level.

How should the p-value be read?

The unadjusted p-value for the posted comparison is 0.743. In general, a p-value describes how unusual data at least as inconsistent with a specified null model would be if that null model and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-value is consistent with the confidence interval’s indication that the data do not clearly distinguish the sequence groups.

The comparison also reports a risk ratio and an odds ratio. A risk ratio compares the response proportions directly, while an odds ratio compares the odds of response. These are distinct effect scales and should not be treated as interchangeable. The risk ratio is 1.114, with a 95% confidence interval from 0.584 to 2.122. The odds ratio is 1.167, with a 95% confidence interval from 0.464 to 2.934. Each interval includes its scale’s null value, and each is wide enough to reflect substantial uncertainty.

Why does over-dispersion matter in general?

For a binary outcome, a simple model may assume that participants’ outcomes vary according to a common response probability. In general, over-dispersion means that the observed variation is greater than such a model expects. If it is ignored where present, uncertainty can be understated and intervals or tests can be too optimistic. The registry record does not report whether over-dispersion was assessed, whether a model was used, or which variance method produced the posted comparison. No particular over-dispersion issue can therefore be asserted for this trial.

What does the crossover design imply?

In general, crossover designs allow participants to receive treatments in sequence, which can make the interpretation dependent on treatment period, timing, and the effects of earlier exposure. Progression or intolerance can determine when a participant switches, so the later treatment period may involve a different clinical state from the first. Carryover refers generally to an effect of an earlier treatment that persists into a later period. It can complicate attribution of an outcome to one treatment if the analysis does not account for it.

The registry identifies the study as crossover and describes two opposite treatment sequences, but it does not report the analysis model, a carryover assessment, or separate estimates for each treatment period. The response-rate summaries should therefore be read as results for the recorded sequence groups, not assumed to be isolated estimates of each drug’s effect independent of order and prior treatment.

What information is missing about the analysis?

The registry record does not report the original statistical analysis plan, the method used to construct the confidence intervals, the test used for the comparison, or any covariate adjustment. It lists zero posted analyses in its analysis information. This does not establish that no analyses were conducted; it means detailed analyses are not available in the registry record. The reported comparison is identified as unadjusted, and no adjusted result is posted.

Likewise, the trial’s original sample-size justification and design assumptions are not reported in the registry record. The separate planning illustration uses the observed effect as its reference and should not be confused with the trial’s original design or with an estimate of the trial’s power after completion. The planning assumptions and their role are described in the sample-size discussion.

10. Confidence Intervals and Precision

The response-rate estimates are 28.0% for Arm A and 31.0% for Arm B. Their 95% confidence intervals are 16.0% to 42.0% and 18.0% to 45.0%, respectively. These ranges are broad relative to the point estimates, indicating that the observed response proportions are not estimated with high precision. The interval endpoints reflect uncertainty in each arm’s response proportion, rather than uncertainty about individual participants’ outcomes.

The between-sequence comparison is also imprecise. Its risk-difference confidence interval extends from a negative value to a positive value, so it includes no difference and differences in either direction. The risk-ratio and odds-ratio intervals likewise include their respective null values. The point estimates are close to one another, but the confidence intervals allow a range of effects wider than the point estimates might suggest when read alone.

Precision depends in part on the amount of outcome information. The response denominators are 42 and 44, and the registry states that patients removed before evaluation were excluded. The record does not give the number or reasons for those exclusions, so their contribution to the precision and possible representativeness of the estimates cannot be assessed from the posted data.

In general, an interval that crosses a null value is not proof of equivalence. Demonstrating equivalence requires a prespecified margin and an analysis designed for that question. Such a margin and an equivalence analysis are not reported in the registry record. The appropriate reading is that the available estimates do not clearly establish a difference, while the intervals remain compatible with more than one underlying effect.

11. Planning a Similar Trial: Sample Size

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

The planning figures are illustrative calculations based on the observed effect, not the trial’s original design assumptions. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a target effect set to a stated fraction of the observed effect. The registry’s original sample-size justification and design assumptions are not reported in the registry record.

For this binary outcome, the figures are participants per arm, not total events. The 80% power column gives the number of participants per arm in the planning calculation for a design with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column gives the corresponding number for a 90% chance under those same conditions. These are prospective design concepts, not descriptions of what happened in this completed trial.

The displayed scenarios are planning for 100% of the observed effect, planning for 75% of the observed effect, and planning for 50% of the observed effect. For those scenarios, the 80% power figures are 3,138, 5,536, and 12,359 participants per arm, respectively. The corresponding 90% power figures are 4,200, 7,411, and 16,544 participants per arm. Smaller effects require more participants because they are harder to distinguish from sampling variation, all else equal.

These calculations are not observed power. They do not show the probability that the completed trial succeeded, nor do they revise the uncertainty in the posted effect estimate. In particular, the scenarios inherit the observed effect as their reference, which is itself uncertain. They are best read as planning illustrations under the stated assumptions, not as a recommended enrollment target or a judgment about the trial’s original design.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.286; treatment proportion p₁ = 0.318; average p̄ = 0.302.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6493 = 1.2725.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6489 = 0.5461.
4. n = (1.2725 + 0.5461)² / (0.0325)² = 3,137.6, rounded up to 3,138 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 <- 0.285714285714286                          # control proportion
p1 <- 0.318181818181818                          # 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(193037)
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 = 3,138 (80% power), 4,200 (90% power)
 75% of observed effect: n per arm = 5,536 (80% power), 7,411 (90% power)
 50% of observed effect: n per arm = 12,359 (80% power), 16,544 (90% power)
power.prop.test: 3137.6 
Simulated power at n = 3,138 per arm: 0.805 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity plan addressing the number of endpoints, comparisons, or analyses. This matters generally because conducting several statistical tests can increase the chance of at least one apparently notable result by chance. Whether adjustment is needed depends on the prespecified testing strategy and the purpose of each analysis; that strategy is not reported in the registry record. The posted primary comparison is identified as unadjusted, with p = 0.743.

The registry lists overall response rate as the primary outcome and progression-free survival as a secondary outcome. It gives one secondary outcome description, but no numerical PFS result is posted. The record also describes possible cross-resistance as an exploratory aim without posting a numerical cross-resistance result. The original hierarchy among outcomes, any planned subgroup analyses, interim analyses, and any adjustment for multiple testing are not reported in the registry record.

For the response analysis, the population description states that patients removed from treatment before evaluation were not included. The denominators are 42 for Arm A and 44 for Arm B, while enrollment was 102. Reasons for exclusion, the number excluded before assessment, and the outcome status of excluded participants are not reported. This exclusion rule means that the primary outcome summaries do not represent every enrolled participant. Whether exclusion could have affected comparisons depends on why participants were removed and how that differed between arms; those details are unavailable.

The record does not report methods for handling other missing data, such as incomplete follow-up or an unassessable response, nor does it describe sensitivity analyses. It also does not specify whether the reported analysis followed an intention-to-treat principle or another analysis population. These gaps prevent a full assessment of missing-data assumptions and population selection.

More generally, missingness can affect a treatment comparison if the likelihood of having an evaluable outcome is related to treatment assignment or response. That is a general methodological concern, not evidence that such a bias occurred in this study. The registry record does not provide enough detail to determine the direction or extent of any effect.

14. 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: progressive disease (9.6%), diarrhea (4.0%), dyspnea (3.8%), pleural effusion (2.0%), failure to thrive (2.0%).

The serious adverse event summary gives 50 participants at risk in Arm A, with 18 affected, and 52 at risk in Arm B, with 22 affected. For other adverse events, the summary gives 50 at risk and 21 affected in Arm A, and 52 at risk and 35 affected in Arm B. These counts are presented separately from the primary response analysis, whose denominators were 42 and 44.

The registry lists the leading serious adverse event terms with percentages: Progressive Disease, 9.6%; Diarrhea, 4.0%; Dyspnea, 3.8%; Pleural Effusion, 2.0%; Failure to Thrive, 2.0%; and Pain - Bone, 2.0%. The record does not specify the denominator for these term percentages in the posted summary. The percentages should therefore be read as the registry’s reported term frequencies, not converted into participant counts or assumed to use the response-analysis population.

In general, an adverse event term is a report of an event category and does not by itself establish that a treatment caused the event. The registry’s adverse event counts do not provide a direct causal comparison. Death counts are not reported in the registry record. These summaries should be considered alongside the study’s crossover structure and differing exposure periods; detailed event timing, attribution, and exposure-adjusted analyses are not reported.

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

The posted results show overall response rates of 28.0% in the sequence beginning with liposomal doxorubicin and 31.0% in the sequence beginning with docetaxel. The comparison has an unadjusted p-value of 0.743, and the confidence intervals for the between-sequence measures include their null values. The data therefore do not clearly distinguish the reported response rates between the two randomized sequences.

That finding is not proof that the sequences are equivalent or that their true response rates are identical. The confidence intervals are broad, and the comparison is compatible with a range of differences. The registry does not report an equivalence margin or an equivalence analysis. The result should be understood as limited evidence for a difference in this comparison, rather than conclusive evidence for no difference.

The outcome is objective response, not duration of response, progression-free survival, overall survival, quality of life, or toxicity-adjusted benefit. Although the registry lists PFS as a secondary outcome, it does not post a numerical PFS result. No numerical result for cross-resistance is reported either. Conclusions about those outcomes cannot be drawn from the response percentages.

The analysis excluded patients removed from treatment before evaluation. Consequently, the percentages describe the analyzed participants and do not directly describe all 102 enrolled participants. The number and reasons for exclusions are not reported. In addition, because the study involved crossover, the sequence-level estimates should not automatically be attributed to the first assigned drug alone; the contribution of treatment periods to the response outcome is not specified.

These results describe what was recorded for this phase II randomized crossover study. They do not establish a general treatment recommendation or resolve how the two drugs compare under other patient populations, treatment schedules, or outcome definitions. The most defensible statistical conclusion is about the posted response proportions and their uncertainty, with the design and analysis-reporting limitations kept in view.

16. Why This Trial Matters Statistically

This trial is statistically notable because it compares treatment sequences in a crossover design while reporting a binary response endpoint. The randomized starting order creates a direct sequence comparison, but the possibility of switching treatment means that the response summaries need careful interpretation. In general, crossover data can contain information about more than one treatment period, yet separating treatment, period, and carryover effects requires appropriate design and analysis details.

The registry reports arm-specific response estimates with confidence intervals and a between-sequence comparison. Reading the point estimates alone might make the groups appear similar, but the intervals show that the estimates are uncertain. The unadjusted p-value does not establish equality; it indicates that the posted comparison does not provide strong evidence against the null under the test used. The distinction between lack of clear evidence for a difference and evidence of equivalence is central to interpreting this result.

The exclusions from the response analysis also matter. The enrolled population was 102, while the response denominators were 42 and 44, and patients removed before evaluation were excluded. Without reasons and counts for those exclusions, readers cannot judge whether the analyzed participants adequately represent all enrolled participants for the outcome of interest.

Finally, the registry states that PFS was a secondary outcome and possible cross-resistance was to be explored, but numerical results for these aims are not posted. The record thus illustrates an important reporting distinction: an aim listed in a trial description is not the same as an available analyzed result. For statistical readers, the principal lesson is to align each conclusion with the endpoint, analysis population, precision, and design details that are actually documented.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary analysis excludes patients removed from treatment before evaluation, but the registry does not report how many participants were excluded or why. The response analysis denominators, 42 and 44, are below the enrollment of 102. Without a fuller disposition of participants, the potential effect of exclusions on the response estimates cannot be evaluated.

The study is identified as crossover, with treatment switching after progression or patient intolerance. However, the record does not specify whether the primary response assessment represents the first treatment period, later treatment, or both. It also does not report period-specific results, an analysis of carryover, or a model for the sequence structure. These omissions constrain attribution of response differences to the initial assigned treatment.

Although the registry lists progression-free survival as a secondary outcome, a numerical PFS result is not reported. The stated exploratory interest in cross-resistance also has no numerical result in the registry record. The response endpoint alone cannot answer those questions.

The analysis method is not described in detail. The registry record does not report the test or confidence-interval method, an adjusted analysis, the statistical analysis plan, or the original sample-size justification. It also does not report a multiplicity strategy, interim analyses, or sensitivity analyses. These missing details limit assessment of analytic choices and robustness.

Safety summaries give counts at risk and affected, and percentages for listed serious event terms, but the denominator for the term percentages, event timing, and attribution are not specified in the posted summary. Death counts are not reported in the registry record. Accordingly, the available safety figures provide a limited descriptive view rather than a complete comparative safety analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Doxorubicin HCI Liposome Injection Versus Weekly Docetaxel in Patients First Relapse Metastatic Breast Cancer — NCT00193037.
• Registry record last updated 2013-07-31; status last verified 2013-07.
• Results first posted 2013-07-19.
• 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.

21. Record Summary

The registry describes a completed randomized phase II crossover study in metastatic breast cancer at first relapse, comparing sequences of liposomal doxorubicin and weekly docetaxel. Enrollment was 102. The primary outcome was overall response rate within 18 Months, defined using complete and partial response criteria.

Arm A, liposomal doxorubicin followed by docetaxel, had a response rate of 28.0% among 42 participants. Arm B, docetaxel followed by liposomal doxorubicin, had a response rate of 31.0% among 44 participants. The unadjusted comparison had p = 0.743, and the confidence intervals indicate substantial uncertainty. Patients removed before evaluation were excluded from the response analysis.

The registry lists PFS as a secondary outcome and possible cross-resistance as an exploratory aim, but numerical results for those outcomes are not reported. The crossover-specific analysis details, missing-data methods, and original design assumptions are also not reported in the registry record.