A Study Comparing Eribulin Mesylate and Ixabepilone in Causing or Exacerbating Neuropathy in Participants With Advanced Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing Eribulin Mesylate and Ixabepilone in Causing or Exacerbating Neuropathy in Participants With Advanced Breast Cancer (NCT00879086), a randomized phase 2 study. The primary outcome is Percentage of Participants With Treatment-Emergent Neuropathy Adverse Events (AEs).

2. Clinical Question

3. Trial Design

The registry describes a phase II, multicenter, randomized, open-label study with a parallel-group design. It compared eribulin mesylate with ixabepilone in participants with advanced breast cancer, with neuropathy adverse events as the primary outcome of interest. The study is listed as completed. Enrollment was 104 participants. The record gives a start date of 2009-03-31 and a primary completion date of 2013-04-30.

Randomization is intended, in general, to make the groups comparable at the time of assignment, but the details needed to assess how it was implemented are not reported in the registry record. The allocation ratio, sequence-generation method, concealment procedures, and any stratification factors are not reported in the registry record. Although the design is described as multicenter, the number or identity of sites is not reported in the registry record.

The study was open-label, so participants and study personnel were not masked to the assigned treatment according to the registry description. Whether neuropathy grading or other outcome assessment was performed by masked assessors is not reported in the registry record. The intervention entries identify the two drugs, but the arm descriptions do not give treatment schedules or doses.

The primary safety analysis included 51 participants assigned to eribulin mesylate and 50 assigned to ixabepilone. Its stated population was restricted to randomized participants who received at least one dose and had at least one safety assessment after the first dose. Other reported outcomes may use different populations: for example, the posted objective response and clinical benefit results each use 52 participants per group. The registry does not explain every difference in analysis population in the record. The original sample-size justification and the trial’s planned power 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.

Before assignment: 127 participants were screened. Of these, 104 participants were enrolled and randomized into the study and 23 participants were screen failures (19 failed to meet entrance criteria, 3 failed due to other reason, and 1 failed due to consent withdrawal).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: SAS included all randomized participants who received at least one dose of study medication and who had at least one safety assessment following the first dose of study medication.

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: SAS included all randomized participants who received at least one dose of study medication and who had at least one safety assessment following the first dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Treatment-Emergent Neuropathy Adverse Events (AEs), measured over From administration of first dose up to approximately 5 years.

The primary endpoint was the percentage of participants with treatment-emergent neuropathy adverse events, assessed from administration of the first dose up to approximately 5 years. It measures the proportion of participants in each group who met the registry’s definition of a treatment-emergent neuropathy event; it is not a measure of neuropathy severity alone or of every possible treatment-related harm.

The registry states that events were graded using National Cancer Institute Common Terminology Criteria for Adverse Events version 3.0 and coded using the current version of the Medical Dictionary for Regulatory Activities. The event definition included the broad list of preferred terms in the Standard MedDRA Query for Neuropathy, along with neuropathy, hyperesthesia, painful response to normal stimuli, pallanesthesia, and allodynia. An event was considered treatment-emergent when the post-baseline maximum CTCAE grade for the combined term neuropathy exceeded its baseline maximum grade.

For an individual participant, a recurring neuropathy event counted once, even if it appeared under different preferred terms, and only the highest grade was counted when grades differed. This rule gives a participant-level percentage rather than a count of repeated episodes. In general, a binary percentage is useful for a direct comparison of how many participants experienced a defined event, but it does not capture when events began, how long they lasted, or the full distribution of grades. Those details are not reported as part of the primary endpoint result.

7. Results Posted in the Registry

• Ixabepilone: 50.0% (25/50) versus 33.3% (17/51) on control; risk difference 16.7 percentage points (95% CI -2.3 to 35.6), risk ratio 1.50 (0.93–2.42); unadjusted two-proportion z-test p = 0.089.

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.

Percentage of Participants With an Incidence of Treatment-emergent Myalgia/Arthralgia

• 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:
  • Ixabepilone: 38.0% (19/50) versus 19.6% (10/51) on control; risk difference 18.4 percentage points (95% CI 1.1 to 35.7), risk ratio 1.94 (1.00–3.75); unadjusted two-proportion z-test p = 0.041.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ixabepilone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Objective Response Rate (ORR)

• 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:
  • Ixabepilone: 5.8% (3/52) versus 15.4% (8/52) on control; risk difference -9.6 percentage points (95% CI -21.3 to 2.1), risk ratio 0.38 (0.11–1.34); unadjusted two-proportion z-test p = 0.111.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ixabepilone and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Benefit Rate (CBR)

• 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:
  • Ixabepilone: 21.2% (11/52) versus 26.9% (14/52) on control; risk difference -5.8 percentage points (95% CI -22.2 to 10.6), risk ratio 0.79 (0.39–1.57); unadjusted two-proportion z-test p = 0.491.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ixabepilone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several distinct domains: treatment-emergent myalgia/arthralgia, vibration perception threshold, participant-reported sensory and motor neurotoxicity, objective response rate, progression-free survival, and clinical benefit rate. The registry lists 10 secondary outcomes as posted. The available numeric results include myalgia/arthralgia, objective response, and clinical benefit; no numeric results for the other named secondary measures are included in this record.

Across the available secondary results, the observed patterns do not all point in one direction. The reported myalgia/arthralgia comparison is higher in the ixabepilone group, while the posted objective response and clinical benefit percentages are higher in the eribulin mesylate group. These outcomes concern different events and use different analysis populations, so they should not be combined into a single overall measure or read as direct confirmation of the neuropathy comparison. The primary result remains the comparison of treatment-emergent neuropathy adverse events; secondary results add context but do not replace it.

The registry reports a Cochran-Mantel-Haenszel analysis for myalgia/arthralgia, with a difference of -18.4, a 95% confidence interval from -36.0 to -0.3, and p =0.049 in the reported group order. The objective response and clinical benefit entries do not include registry-reported comparative analyses. Any unadjusted calculations for those outcomes are therefore descriptive rather than a reported confirmatory analysis.

In general, when many outcomes are examined, some may appear notable by chance even if there is no underlying difference for those outcomes. An adjustment strategy or prespecified hierarchy can help control that issue, but a multiplicity plan is not reported in the registry record. The secondary results should consequently carry less inferential weight than a prespecified primary analysis and should be interpreted cautiously, particularly where only a single unadjusted comparison is available. The original analysis plan and the rationale for the outcome hierarchy are not reported in the registry record.

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

• Percentage of Participants With an Incidence of Treatment-emergent Myalgia/Arthralgia
• Change From Baseline in Vibration Perception Threshold (VPT)
• Number of Participants With Shift From Baseline to Worst Post-baseline Participant Neurotoxicity Questionnaire (PNQ) Score for Item 1 (Sensory)
• Number of Participants With Shift From Baseline to Worst Post-baseline Participant Neurotoxicity Questionnaire (PNQ) Score for Item 2 (Motor)
• Number of Participants With Shift From Baseline to Worst Post-baseline Participant Neurotoxicity Questionnaire (PNQ) Composite Score
• Objective Response Rate (ORR)
• Progression-Free Survival (PFS)
• Clinical Benefit Rate (CBR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either met the defined treatment-emergent neuropathy criterion or did not. The arm percentages therefore describe the proportion with at least one qualifying event under the registry’s counting rules. For this endpoint, a participant with repeated qualifying neuropathy events was counted once, and the highest CTCAE grade was retained when more than one grade occurred.

What does the risk difference describe?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the other. Its units are percentage points when the proportions are presented as percentages. The sign depends on which group is subtracted from which, so the group order must be stated. The recalculated comparison uses ixabepilone minus eribulin mesylate and is positive because the posted percentage is higher in the ixabepilone group. The registry’s reported analysis lists eribulin mesylate first and ixabepilone second, giving the difference the opposite sign. Reversing the order changes the sign but not the underlying comparison.

What does a confidence interval add?

In general, a confidence interval conveys the range of effect estimates compatible with the data under the method used, along with the interval procedure’s assumptions. It communicates uncertainty more directly than a single point estimate. For the registry’s primary comparison, the reported 95% confidence interval runs from -36.1 to 2.4 for the listed group order. The interval includes zero, the value corresponding to no difference. The unadjusted recalculation also has an interval that includes zero. Neither interval establishes that the true difference is zero; rather, the data do not rule out no difference under those analyses. The width also indicates that the estimate is not highly precise.

Why are there two comparative results?

The registry reports a Cochran-Mantel-Haenszel analysis of the difference in proportions, with a reported value of -16.7, a 95% confidence interval from -36.1 to 2.4, and p =0.094. The separate recalculation is a simple unadjusted comparison of the posted summary proportions. Such calculations can differ because they use different analysis procedures or conventions. The reported analysis is the registry’s own result; the recalculation is a supplemental, unadjusted reading of the posted counts and proportions. The registry does not provide enough detail to reconstruct every aspect of its analysis procedure.

What does the p-value mean?

In general, a p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the analysis assumptions were true. 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 registry reports p =0.094 for its primary comparison, while the unadjusted recalculation gives p =0.089. These values do not cross the conventional 0.05 threshold, but the threshold does not determine whether an estimate is important or whether a treatment is effective. Interpretation should consider the estimate, its interval, the design, and the outcome definition together.

Why can over-dispersion matter?

In general, over-dispersion means observed variability is greater than a statistical model expects. It can make standard errors and confidence intervals too small if the analysis assumes less variability than is present. This concept is most relevant to outcomes modeled as counts or rates; the primary endpoint is a binary participant-level percentage. The registry does not report an over-dispersion assessment for this endpoint, and there is no basis in the record to claim that over-dispersion affected the posted primary result.

How should the analysis population be understood?

The primary safety population included all randomized participants who received at least one dose and had at least one safety assessment following the first dose. Thus, it was not simply everyone enrolled or necessarily everyone randomized. The record reports 51 participants in the eribulin mesylate analysis group and 50 in the ixabepilone analysis group. In general, defining an analysis population can affect the interpretation of a treatment comparison, particularly if participants are excluded after randomization. The reasons some randomized participants may not have entered this analysis are not reported in the registry record.

The definition also requires a post-dose safety assessment. The record does not describe how participants without such an assessment were handled, whether any endpoint data were imputed, or how incomplete follow-up was addressed. Those omissions make it difficult to judge the possible influence of missing data. The stated timeframe extends from first dose up to approximately 5 years, but the primary result is a participant-level percentage and is not a time-to-event estimate.

How do secondary tests fit in?

In general, testing several outcomes increases the chance that at least one result appears statistically notable by chance when each is considered separately. Methods that adjust for multiplicity can address that issue, but the registry does not report an adjustment plan for the posted secondary analyses. The secondary myalgia/arthralgia result has a registry-reported Cochran-Mantel-Haenszel analysis; the objective response and clinical benefit entries do not list corresponding reported analyses. Unadjusted recalculations of those entries are descriptive and should not be treated as confirmatory evidence. The original statistical analysis plan, including any prespecified hierarchy or multiplicity procedure, is not reported in the registry record.

11. Confidence Intervals and Precision

The primary arm estimates are 33.3% for eribulin mesylate, with a 95% confidence interval from 20.8 to 47.9, and 50.0% for ixabepilone, with a 95% confidence interval from 35.5 to 64.5. Each arm’s interval is broad, reflecting uncertainty in the estimated percentage. The intervals overlap, but overlap between separate arm intervals is not itself a formal test of the difference. The direct comparative analysis and its confidence interval are more appropriate for assessing the contrast between groups.

The registry’s reported difference is -16.7, with a 95% confidence interval from -36.1 to 2.4. The recalculated comparison in the reverse direction has a 95% confidence interval from -2.3 to 35.6 percentage points. The direction differs because the group order differs. Both intervals include a value corresponding to no difference, and both allow a range of comparative effects. In general, a 95% confidence interval gives a sense of precision under the analysis assumptions; it does not guarantee that the true effect lies within any one calculated interval.

The primary analysis includes 51 participants in one arm and 50 in the other. With this size of analysis population, a percentage can shift noticeably when the event status of a participant changes, and the intervals communicate that sampling uncertainty. The record does not report interval-method details beyond the stated 95% confidence level and the registry’s analysis method. It also does not provide enough information to assess precision under alternative missing-data assumptions or to evaluate whether all randomized participants contributed endpoint data.

Precision is distinct from statistical significance. A confidence interval that includes no difference does not prove the groups are identical, just as an interval excluding no difference would not by itself establish clinical importance. Here, the interval includes no difference and spans effects in both directions. The estimate should therefore be read as suggestive of a direction in the observed data but imprecise as a measure of the underlying comparative effect.

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. The registry does not report the original sample-size assumptions. The stated illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For binary outcomes, the displayed figures are participants per arm. For time-to-event outcomes, the sample-size convention is total events, though the primary endpoint is binary.

The 80% power column means the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions are correct. The 90% power column uses a higher target chance of detecting that effect, and therefore generally calls for more participants. These are planning targets, not guarantees that a future study will detect an effect.

For the primary comparison, the illustration gives 137 participants per arm when planning for 100% of the observed effect, 240 participants per arm for 75% of the observed effect, and 529 participants per arm for 50% of the observed effect at the 80% target. At the 90% target, the corresponding figures are 182, 320, and 708 participants per arm. The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation and require more participants under otherwise similar assumptions.

These figures are not observed power. They do not describe the probability that the completed study found an effect, nor do they establish that the original trial was adequately planned. They are conditional planning illustrations built from the observed effect, which itself is uncertain. The trial’s own design assumptions and sample-size justification are not reported in the registry record.

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 = 0.333; treatment proportion p₁ = 0.500; average p̄ = 0.417.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6972 = 1.3665.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6872 = 0.5783.
4. n = (1.3665 + 0.5783)² / (0.1667)² = 136.2, rounded up to 137 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 <- 0.333333333333333                          # control proportion
p1 <- 0.5                          # 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(879086)
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 = 137 (80% power), 182 (90% power)
 75% of observed effect: n per arm = 240 (80% power), 320 (90% power)
 50% of observed effect: n per arm = 529 (80% power), 708 (90% power)
power.prop.test: 136.2 
Simulated power at n = 137 per arm: 0.806 (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 primary analysis uses a Cochran-Mantel-Haenszel method and lists the groups in the order eribulin mesylate followed by ixabepilone. It reports a difference in proportions of -16.7, a 95% confidence interval from -36.1 to 2.4, and p =0.094. The negative direction is consistent with a higher posted event percentage in the ixabepilone group when the difference is expressed as eribulin mesylate minus ixabepilone.

The unadjusted recalculation is expressed in the reverse order, ixabepilone minus eribulin mesylate. It gives a positive risk difference of 16.7 percentage points, a confidence interval from -2.3 to 35.6 percentage points, and p =0.089. The two results tell a similar broad story: the observed proportions differ in the same direction once group order is taken into account, and the comparative intervals include no difference. Their numerical values are not identical, which can occur when the registry’s analysis method and the simple unadjusted recalculation differ.

The registry’s own analysis is the primary reported inferential result. The recalculation is a supplementary comparison from the posted summary statistics, not a replacement for the sponsor’s analysis. The registry record does not give enough detail to reproduce every aspect of the Cochran-Mantel-Haenszel procedure or its inputs.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and multiple secondary outcomes. The primary outcome is the percentage of participants with treatment-emergent neuropathy adverse events. Secondary outcomes include musculoskeletal symptoms, vibration perception threshold, participant-reported neurotoxicity, response, progression-free survival, and clinical benefit. With multiple outcomes, the chance of at least one apparently notable finding can increase if each is tested separately. In general, multiplicity procedures or a prespecified testing hierarchy can help manage that concern. Whether this trial used such a procedure is not reported in the registry record.

The record posts a sponsor analysis for the primary endpoint and for myalgia/arthralgia. It does not list corresponding sponsor analyses for objective response or clinical benefit. No inferential results are included for several named secondary measures. The statistical analysis plan, including details of endpoint prioritization, any interim analyses, and any multiplicity adjustment, is not reported in the registry record. These missing details limit assessment of which findings were confirmatory and how the full set of outcomes was handled.

The primary safety population is defined as all randomized participants who received at least one dose and had at least one safety assessment after the first dose. The record does not describe the number or reasons for participants who may have been randomized but excluded from that population. It also does not describe the handling of participants with incomplete safety follow-up, missing endpoint assessments, or missing baseline grades. Imputation methods and sensitivity analyses for missing data are not reported in the registry record.

Different outcome entries have different denominators: the primary safety analysis includes 51 participants in the eribulin mesylate group and 50 in the ixabepilone group, while the posted response and clinical benefit results use 52 participants in each group. The registry does not explain these analysis-population differences in the record. They should be kept in mind when comparing outcomes, because results with different denominators need not describe precisely the same participant sets. Further detail about adherence to assigned treatment, protocol deviations, and analysis populations is not reported in the registry record.

16. 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: febrile neutropenia (11.8%), hypercalcaemia (4.0%), sepsis (3.9%), metastases to central nervous system (3.9%), malignant neoplasm progression (3.9%).

The serious adverse event summary lists 51 participants at risk in the eribulin mesylate group, with 19 affected, and 50 at risk in the ixabepilone group, with 17 affected. The record also lists 2 deaths in each group. These counts describe the posted serious adverse event summary; the record does not provide enough detail to attribute each event to treatment or establish a comparative causal effect.

For other adverse events, the listed counts are 51 of 51 in the eribulin mesylate group and 50 of 50 in the ixabepilone group. These figures indicate that the record reports at least one other adverse event for every participant in the corresponding at-risk group, but the summary does not establish severity or relatedness for each event. The serious-event terms listed include febrile neutropenia, hypercalcaemia, sepsis, metastases to central nervous system, malignant neoplasm progression, and anaemia. The listed percentages are not presented by treatment group in this summary, so they should not be interpreted as arm-specific comparisons.

Adverse event counts and the primary neuropathy endpoint answer different questions. The neuropathy endpoint uses its own event definition and participant-level counting rule. The serious adverse event summary should be read as a separate descriptive safety overview, not as a substitute for the primary analysis or a complete account of the benefit-risk profile. Additional detail about seriousness criteria, relatedness assessments, event timing, and treatment discontinuations is not reported in the registry record.

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

The primary result describes the proportion of analyzed participants who met a specific treatment-emergent neuropathy definition. The observed percentage was 33.3% with eribulin mesylate and 50.0% with ixabepilone. The registry’s comparison and the unadjusted recalculation both have confidence intervals that include no difference. The data therefore do not provide a precise estimate that clearly separates the groups under these analyses.

This does not mean the groups have been shown to be identical. A non-significant result can reflect uncertainty as well as the possibility of little or no difference. The registry does not report an equivalence or non-inferiority design, so equivalence cannot be concluded. Conversely, the higher observed percentage in one group does not by itself establish a causal treatment effect or its clinical importance.

The endpoint is specific to treatment-emergent neuropathy as operationalized with the CTCAE grading rule and the designated MedDRA terms. It does not cover every possible neurological symptom, all adverse events, or the complete severity and duration profile of neuropathy. The primary result is a participant percentage, not a time-to-onset or event-duration analysis.

Other posted outcomes address symptoms and measures of cancer response, but they have different definitions and, in some cases, different analysis populations. Their results do not prove or disprove the primary safety finding. The registry does not report a multiplicity plan, complete missing-data procedures, or full details of the original statistical analysis plan, which limits how firmly secondary comparisons can be interpreted.

Overall, the registry documents a randomized comparison and a higher observed neuropathy percentage in the ixabepilone group, alongside substantial uncertainty in the comparative estimate. These results describe the posted analyses; they do not determine which treatment is appropriate for an individual or provide medical advice. A fuller interpretation would require details about treatment delivery, participant flow, follow-up completeness, outcome assessment, and the prespecified analysis plan, several of which are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a comparison of two percentages should be accompanied by a direct effect estimate and its uncertainty. The observed arm percentages differ, but the confidence interval for the comparative effect includes no difference. Looking only at the arm percentages could overstate how clearly the data distinguish the groups; looking only at a p-value would conceal the range of effects compatible with the analysis.

It also illustrates the importance of specifying outcome definitions. The neuropathy result depends on a defined set of coded events, a baseline-to-post-baseline grade comparison, and a rule that counts repeated events once per participant while retaining only the highest grade. Those choices determine what the percentage represents. Another event definition or a severity-focused outcome would answer a different question.

Analysis populations matter as well. The primary safety percentages use participants with at least one dose and a post-dose safety assessment, while some secondary outcomes use different denominators. A clear account of participant flow and missing data is important for judging whether the analyzed groups remain comparable after randomization. Those details are incomplete in the registry record.

Finally, several secondary outcomes and safety summaries appear alongside the primary result. Without a reported multiplicity plan and fuller analysis details, isolated secondary findings should not be given the same weight as a prespecified primary comparison. The trial is a useful example of how statistical interpretation depends not only on the observed numbers, but also on design, endpoint construction, analysis populations, uncertainty, and the completeness of reporting.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry identifies the study as randomized, multicenter, open-label, and parallel-group, but important design details are not reported in the registry record. These include the randomization procedure, allocation concealment, allocation ratio, stratification, treatment doses and schedules, and whether outcome assessment was masked. The original sample-size justification and intended statistical power are also not reported in the registry record.

The primary result is based on a safety population requiring at least one dose and at least one safety assessment after the first dose, rather than necessarily all randomized participants. The registry does not report participant flow, reasons for exclusion from the safety analysis, the extent of incomplete follow-up, or the method for handling missing endpoint data. These gaps make it harder to assess potential post-randomization selection and the robustness of the estimate.

The endpoint relies on CTCAE grading and a set of coded terms, with a specified baseline comparison and participant-level counting rule. The registry does not provide detailed participant-level grade distributions, event timing, duration, or the results of the other listed neurotoxicity measures in the record. The open-label design may be relevant to assessment and reporting of subjective symptoms; whether assessors were masked is not reported in the registry record.

The primary comparative confidence interval includes no difference and is broad. The secondary outcome analyses also have limitations: the registry does not report a multiplicity plan, and it does not provide a sponsor comparative analysis for every posted secondary outcome. Some secondary outcomes use a different number of participants from the primary safety analysis. The record does not explain those differences or provide a complete statistical analysis plan, so the strength and intended status of individual findings remain uncertain.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Comparing Eribulin Mesylate and Ixabepilone in Causing or Exacerbating Neuropathy in Participants With Advanced Breast Cancer — NCT00879086.
• Registry record last updated 2023-06-22; status last verified 2021-10.
• Results first posted 2021-12-01.
• 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 NCT00879086 as a completed phase II, multicenter, randomized, open-label, parallel-group study comparing eribulin mesylate with ixabepilone in participants with advanced breast cancer. Enrollment was 104. The listed study start date is 2009-03-31, and the primary completion date is 2013-04-30.

The primary endpoint was the percentage of participants with treatment-emergent neuropathy adverse events, assessed from first dose up to approximately 5 years. The safety analysis included 51 participants in the eribulin mesylate group and 50 in the ixabepilone group. The posted percentages were 33.3% and 50.0%, respectively. The registry’s comparative analysis reported a difference of -16.7, a 95% confidence interval from -36.1 to 2.4, and p =0.094 in the stated group order.

The record also lists secondary outcomes and adverse event summaries. The original sample-size justification, detailed missing-data procedures, multiplicity plan, and full statistical analysis plan are not reported in the registry record. The primary comparison is therefore best read as an uncertain estimate from the posted analysis population, rather than a definitive conclusion about a treatment difference.