Zoledronic Acid in Treating Patients With Metastatic Breast Cancer, Metastatic Prostate Cancer, or Multiple Myeloma With Bone Involvement: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Zoledronic Acid in Treating Patients With Metastatic Breast Cancer, Metastatic Prostate Cancer, or Multiple Myeloma With Bone Involvement (NCT00869206), a randomized phase 3 study. The primary outcome is Percentage of Participants With at Least One Skeletal-related Event (SRE) Within 2 Years After Randomization.

2. Clinical Question

The clinical question concerns the interval between doses, not a comparison of zoledronic acid with no treatment or with a different drug. Both groups received the same drug, and the intended contrast was a less frequent versus more frequent schedule. The registry describes the primary objective as a non-inferiority comparison. It does not report the non-inferiority margin, which is necessary to define how much difference would be considered acceptable for that purpose.

The registry describes bone-related complications as a major cause of morbidity in these metastatic cancers. The primary outcome therefore focuses on whether participants experienced at least one such event during the specified follow-up period. The specific events included in the registry's SRE definition are not reported in the registry record. The question applies to the stated cancer groups with bone involvement; it does not establish that results are the same for each cancer type separately.

3. Trial Design

This was a randomized, phase III, parallel-group study with 1,822 participants enrolled. The registry reports no masking. One group was assigned zoledronic acid every 4 weeks and the other every 12 weeks. Treatment could continue for up to 2 years, subject to disease progression or unacceptable toxicity. The trial is listed as completed.

The primary outcome was assessed within 2 years after randomization. The registry describes the primary analysis population as all patients who were eligible and completed treatment. The posted primary arm results each use 911 participants. That population description is important: it is not the same wording as an analysis of every randomized participant regardless of treatment completion.

The registry record does not report the randomization procedure, allocation concealment, stratification factors, or the planned analysis population beyond the eligible-and-completed description. The trial's original sample-size justification and design assumptions are not reported in the registry record. The posted planning illustrations are calculations based on observed effects and should not be taken as the trial's original design rationale.

The study included secondary outcomes addressing pain, performance status, osteonecrosis of the jaw, renal dysfunction, skeletal morbidity, and other measures. The registry lists 12 outcome measures, and results are posted for 11 secondary outcomes. The registry record does not provide a complete account of how outcomes were prioritized or how the secondary analyses were coordinated.

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

Analysis population for the primary outcome, as defined in the registry: All patients that were eligible and completed treatment were analyzed.

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: All baseline patients demographics were analyzed.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With at Least One Skeletal-related Event (SRE) Within 2 Years After Randomization, measured over 2 years.

The primary endpoint is the percentage of participants with at least one skeletal-related event within 2 years after randomization. It is a binary outcome at the participant level: each participant is classified according to whether at least one event occurred during that period. The registry does not report the specific event components included in its SRE definition, so the endpoint should be interpreted using the registry's label rather than an assumed list of complications.

For the every-4-week group, the posted result is 67.6%; for the every-12-week group, it is 67.9%. The posted counts are 616 events among 911 participants and 619 among 911 participants, respectively. These values describe the observed proportions in the stated analysis population; they do not by themselves establish non-inferiority or equivalence.

A binary endpoint of this kind is useful for expressing how many participants experienced at least one event, rather than how many total events occurred. It treats a participant with one event and a participant with multiple events alike for this particular measure. The registry also lists skeletal morbidity rate as a secondary outcome, which is a distinct outcome label. Bone-related complications are described in the registry as a major source of morbidity in these patient groups, giving the event-based endpoint a direct connection to the trial's stated clinical question.

7. Results Posted in the Registry

• Arm II (Zoledronic Acid Every 12 Weeks): 67.9% (619/911) versus 67.6% (616/911) on control; risk difference 0.3 percentage points (95% CI -4.0 to 4.6), risk ratio 1.00 (0.94–1.07); unadjusted two-proportion z-test p = 0.880.

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.

Average Pain Intensity Score as Assessed by the Brief Pain Inventory (BPI) Questionnaire

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Arm II (Zoledronic Acid Every 12 Weeks): mean 2.09 versus 2.06 on control; difference 0.03 (95% CI -0.36 to 0.42), standardized effect d = 0.01; z-test p = 0.880.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Zoledronic Acid Every 12 Weeks) and the control. The interval gives the range of effects that remain compatible with the data.

Average ECOG Performance Status

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Arm II (Zoledronic Acid Every 12 Weeks): mean 0.84 versus 0.82 on control; difference 0.02 (95% CI -0.10 to 0.14), standardized effect d = 0.02; z-test p = 0.736.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Zoledronic Acid Every 12 Weeks) and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Osteonecrosis of the Jaw

• 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:
  • Arm II (Zoledronic Acid Every 12 Weeks): 1.0% (9/884) versus 2.0% (18/882) on control; risk difference -1.0 percentage points (95% CI -2.2 to 0.1), risk ratio 0.50 (0.23–1.10); unadjusted two-proportion z-test p = 0.080.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Zoledronic Acid Every 12 Weeks) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains: pain intensity, ECOG performance status, jaw osteonecrosis, renal dysfunction, skeletal morbidity, bone-turnover measurement, and subgroup assessments of SREs. The posted summaries span continuous scores and event proportions. This range helps describe outcomes beyond the primary binary measure, but the secondary results do not replace the primary endpoint or independently resolve its non-inferiority question.

The posted comparisons for pain and ECOG use mixed-model analyses of slope, while the simple recalculations summarize arm-level differences. Those are different summaries and need not produce identical results. The secondary results should be read in the context of their outcome definitions, timeframes, analysis populations, and methods. Further detail on those features is not reported in the registry record for every outcome.

There are multiple secondary outcomes and subgroup questions. When many outcomes are examined, some results may appear notable by chance even if there is no underlying effect. Whether the sponsor adjusted for multiplicity, prioritized particular secondary outcomes, or treated the analyses as exploratory is not reported in the registry record. Unadjusted secondary comparisons therefore carry less weight than a prespecified primary analysis, especially when their estimates are not supported by a stated multiplicity strategy.

The secondary measures may provide context about symptoms, function, safety, and other aspects of skeletal disease, but they should not be combined into a single conclusion without a prespecified analysis plan. They also should not be used to infer that the primary result applies identically to each cancer subgroup. The registry lists subgroup outcomes, but subgroup-specific results and their uncertainty are not fully described in the available record.

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

• Average Pain Intensity Score as Assessed by the Brief Pain Inventory (BPI) Questionnaire
• Average ECOG Performance Status
• Incidence of Osteonecrosis of the Jaw
• Incidence of Renal Dysfunction
• Skeletal Morbidity Rate
• Bone Turnover Assessed by Serum C-telopeptide (CTX) Levels (Breast Cancer)
• Proportion of Patients Having at Least One SRE Within 24 Months After Randomization for the Subgroups of Patients With Breast Cancer
• Proportion of Patients Having at Least One SRE Within 24 Months After Randomization for the Subgroups of Patients With Prostate Cancer

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant experienced at least one SRE during the specified follow-up. The arm percentages are proportions of participants with the event. The unadjusted re-calculation compares those proportions between the two schedules. It is a straightforward summary contrast, not a replacement for the trial's sponsor-reported analysis.

What does a risk difference express?

A risk difference subtracts the event proportion in one group from the event proportion in the other. It remains on the absolute probability scale: zero corresponds to equal proportions, a positive value indicates a higher observed proportion in the group named first in the contrast, and a negative value indicates a lower one. Here the re-calculated risk difference is 0.003 for every-12-week relative to every-4-week dosing. The interval around it extends from -0.040 to 0.046. Since the interval spans zero, it is compatible with either direction of difference as well as no difference, within the uncertainty represented by that interval.

What does the confidence interval add?

A confidence interval describes a range of estimates compatible with the data under the method used and its assumptions. Its purpose is to show precision and plausible uncertainty, rather than to declare that the true value must lie in the range with certainty. The registry record does not state the confidence level for the re-calculated interval. The interval is not a non-inferiority boundary: that requires a prespecified margin, and the margin is not reported in the registry record.

How does the reported analysis differ?

The registry lists a Cochran-Mantel-Haenszel method for the sponsor's primary comparison and labels the analysis as non-inferiority or equivalence. In general, a Cochran-Mantel-Haenszel procedure can combine information across strata while accounting for the stratification used in an analysis. The registry record does not specify the strata or give enough detail to establish which particular implementation was used. It reports p <= .05 but gives no numerical effect estimate or confidence interval for that analysis. Because the posted comparison has a discrepancy flag, the sponsor's own analysis takes precedence over the simple unadjusted re-calculation.

General interpretation of a non-inferiority analysis differs from interpretation of a test for any difference. In a conventional difference test, the null hypothesis commonly concerns no difference. In non-inferiority testing, the question is whether the data rule out a loss greater than a prespecified acceptable margin. The margin and the exact hypothesis tested are essential to interpretation; neither the margin nor a complete numerical report of the sponsor's result is available in the registry record. A reported p value without those details is not sufficient to independently reconstruct the non-inferiority conclusion.

Why can binary outcomes be uncertain?

For a binary endpoint, the observed proportion is affected by the number of participants and the number experiencing the event. Even when arm percentages look close, the estimate has sampling uncertainty. A confidence interval makes that uncertainty more visible. The interval's width depends on the amount of information in the data and the variability inherent in the outcome. This is a general statistical explanation; it does not add assumptions about this trial's design.

The primary summary focuses on whether each person had at least one event, not on the number or timing of repeated events. It consequently does not convey every feature of skeletal morbidity. A separate outcome such as skeletal morbidity rate may address a different aspect, but its name alone does not establish its precise calculation. Further endpoint definitions and analysis details are not reported in the registry record.

Why distinguish recalculation from the trial analysis?

The unadjusted re-calculation uses posted group-level event counts and denominators to describe a simple difference. It does not reproduce any stratification, covariate adjustment, handling of missing outcomes, or other features that may be part of the sponsor's analysis. Those details are not reported sufficiently to reproduce the trial analysis. The re-calculated result is therefore a supplementary summary, not a competing primary analysis. Where the discrepancy flag applies, the sponsor's reported analysis takes precedence.

These distinctions matter because the trial's stated objective is non-inferiority, while the simple re-calculation is a descriptive unadjusted comparison. Similar arm percentages and a re-calculated interval that crosses zero are not, on their own, a formal demonstration of non-inferiority. The margin, analysis population, and sponsor's numerical estimate with uncertainty are central to that judgment, and the available registry entry does not report all of those details.

11. Confidence Intervals and Precision

The re-calculated risk difference for the primary outcome is 0.003, with an interval from -0.040 to 0.046. The point estimate is close to zero, but the interval extends in both directions around zero. This means the posted summary statistics are compatible with a range of possible differences, including a lower event proportion with every-12-week dosing, little or no difference, or a higher event proportion. The interval should not be read as proof of equivalence.

Confidence intervals communicate precision: a narrower interval indicates greater precision under the method's assumptions, while a wider interval leaves more uncertainty about the size and direction of the effect. The registry record does not state the confidence level for this re-calculated interval. It also does not report the sponsor's primary confidence interval or effect estimate, so precision for the sponsor's non-inferiority analysis cannot be assessed from the entry.

For a non-inferiority question, precision must be considered relative to the acceptable margin, not only relative to zero. Since the margin is not reported in the registry record, the interval cannot be compared with the criterion needed to assess non-inferiority. The close observed percentages are useful descriptive information, but the width and placement of an interval relative to a prespecified margin are more relevant to the formal claim.

The primary arm denominators are 911 in each group. The endpoint description limits the analyzed population to eligible patients who completed treatment, and the record does not explain the handling of participants without a complete outcome. That limits how fully the precision and potential selection effects can be evaluated.

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 illustrations use the observed effect as a reference and consider planning for 100% of that effect, 75% of the observed effect, and 50% of the observed effect. For the primary endpoint, the listed values are participants per arm: 316,111 and 423,182 for 80% and 90% power when planning for 100% of the observed effect; 562,352 and 752,828 when planning for 75%; and 1,266,137 and 1,694,997 when planning for 50%.

The 80% power column describes an illustrative sample size per arm that would give an 80% chance of detecting the selected effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column expresses the corresponding illustration for a 90% chance. These figures are per arm, not totals across both groups. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. Smaller effects require more participants, which is why the illustrative requirements increase when the assumed effect is reduced.

These are planning illustrations based on the observed effect, not observed power and not the trial's original sample-size justification. The original design assumptions and sample-size justification are not reported in the registry record. The illustrations should not be read as evidence that the trial was or was not adequately powered for its intended non-inferiority objective.

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 = 0.676; treatment proportion p₁ = 0.679; average p̄ = 0.678.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6609 = 1.2953.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6609 = 0.5562.
4. n = (1.2953 + 0.5562)² / (0.0033)² = 316,110.3, rounded up to 316,111 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 <- 0.676180021953897                          # control proportion
p1 <- 0.6794731064764                          # 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(869206)
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 = 316,111 (80% power), 423,182 (90% power)
 75% of observed effect: n per arm = 562,352 (80% power), 752,828 (90% power)
 50% of observed effect: n per arm = 1,266,137 (80% power), 1,694,997 (90% power)
power.prop.test: 316110.3 
Simulated power at n = 316,111 per arm: 0.795 (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 reports a sponsor analysis of the primary comparison using the Cochran-Mantel-Haenszel method, with the analysis categorized as non-inferiority or equivalence and a reported p value of <= .05. It does not report a numerical effect estimate, confidence interval, or non-inferiority margin for that result. Those omissions prevent an independent reconstruction of the sponsor's formal conclusion from the registry entry alone.

The unadjusted re-calculation uses the posted event counts and arm denominators and gives a risk difference of 0.003, an interval from -0.040 to 0.046, and an unadjusted p value of 0.88. The record flags a discrepancy between the sponsor analysis and the re-calculation. The sponsor's own analysis takes precedence; the simple re-calculation is an additional descriptive check and should not be substituted for the sponsor's method.

The different results cannot be reconciled from the information in the registry record. It does not report the exact test statistic, analysis details, margin, or other information needed to determine the source of the discrepancy. The sponsor's p value should therefore be described as reported, without treating it as interchangeable with the re-calculated p value or inferring the missing effect estimate.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome alongside numerous secondary outcomes, including separate subgroup questions. Testing or estimating many outcomes creates a multiplicity issue: the more comparisons considered, the greater the chance that at least one may look unusual by chance. This is a general statistical concern, not evidence that any particular posted result is false. Whether multiplicity was addressed, and by what method, is not reported in the registry record.

The primary endpoint description says eligible patients who completed treatment were analyzed. The record does not explain how this population was defined in relation to all randomized participants, how treatment completion affected inclusion, or how missing endpoint information was handled. It does not report whether missing outcomes were imputed, excluded, or treated through another approach. These omissions matter because non-inferiority conclusions can be sensitive to analysis population and missing-data assumptions.

The registry gives 911 participants in each primary arm, while the adverse-event summaries use different at-risk denominators. The record does not explain the denominator differences. The primary endpoint's eligible-and-completed wording also means its results should not be assumed to represent every randomized participant without further information.

The registry identifies a Cochran-Mantel-Haenszel analysis for the primary non-inferiority or equivalence comparison but does not report the non-inferiority margin, the primary effect estimate, or its interval. Interim analyses, stopping rules, and the trial's detailed statistical analysis plan are not reported in the registry record. The original sample-size justification is also not reported. These missing details limit assessment of the planned type I error control, the analysis's relationship to the stated objective, and the robustness of the result.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: serum calcium decreased (3.9%), urogenital disorder (2.6%), nausea (1.8%), disease progression (1.7%), death nos (1.6%).

The adverse-event summary reports serious adverse events for 96 of 879 participants at risk in the every-4-week group and 103 of 868 at risk in the every-12-week group. Other adverse events are reported for 779 of 879 and 750 of 868, respectively. Deaths are listed as 41 and 42. These are posted counts with their stated at-risk denominators; they are not rates adjusted for time at risk, and no such adjustment is reported.

The most frequently listed serious terms include serum calcium decreased at 3.9%, urogenital disorder at 2.6%, nausea at 1.8%, disease progression at 1.7%, Death NOS at 1.6%, and constipation at 1.4%. A term appearing in this summary does not by itself establish that the assigned schedule caused it. The registry entry does not give enough information to assess event timing, duration, severity distribution, or comparative statistical uncertainty.

The adverse-event denominators differ from the primary endpoint denominators, and the reason is not reported in the registry record. These summaries describe reported events in the groups; they are not, on their own, a complete comparative safety analysis.

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

The posted primary data show similar observed proportions of participants with at least one SRE within 2 years: 67.6% with dosing every 4 weeks and 67.9% with dosing every 12 weeks. The unadjusted re-calculation gives a small risk difference estimate and an interval that includes zero. These descriptions summarize the posted results; they do not establish that the schedules are equivalent or that one schedule is clinically preferable.

The trial's stated objective is non-inferiority, which requires evaluating the result against an acceptable margin specified in advance. That margin is not reported in the registry record. The sponsor's reported analysis is identified as non-inferiority or equivalence and has p <= .05, but its effect estimate and interval are not provided. The sponsor's own analysis takes precedence over the unadjusted re-calculation, while the limited numerical detail means that the formal conclusion cannot be fully assessed from the registry entry alone.

The result applies to the analysis population described in the registry: eligible patients who completed treatment. It should not be assumed to describe all randomized patients if some did not complete treatment or had missing outcomes. The pooled primary result also does not show whether the outcome differed across breast cancer, prostate cancer, and multiple myeloma subgroups.

The findings do not establish what would happen beyond the reported 2-year timeframe, under different dosing schedules, or in populations not described by the trial. They also do not identify which specific skeletal events made up the endpoint, because that definition is not reported in the registry record. The responsible interpretation is limited to the observed outcomes and the analysis details that the registry reports.

18. Why This Trial Matters Statistically

This trial poses a useful statistical question because it compares two schedules of the same treatment and frames the less frequent schedule as a non-inferiority question. In such a design, a finding of no statistically significant difference under an ordinary difference test would not automatically show that the less frequent schedule meets a non-inferiority criterion. The margin and the uncertainty around the sponsor's effect estimate are essential to interpreting that claim.

The posted primary arm percentages are close, but closeness of point estimates is not the same as precision or proof of equivalence. The unadjusted interval illustrates uncertainty around the simple risk-difference estimate. The sponsor's reported method is the analysis relevant to the stated objective, yet the registry entry does not provide enough numerical detail to reproduce or fully evaluate it. The discrepancy between the sponsor analysis and the simple re-calculation makes it especially important to distinguish a descriptive check from the trial's own analysis.

The study also highlights how analysis populations and outcome definitions affect interpretation. The primary endpoint is described for eligible participants who completed treatment, while the record does not fully explain missing data or the relation of that population to all randomized participants. Secondary outcomes and subgroup questions add useful context but bring multiplicity and interpretation challenges when their analysis plan is not available.

Statistically, the central lesson is not that a particular schedule has been established as equivalent. It is that a non-inferiority claim requires transparent reporting of the margin, analysis population, estimate, and uncertainty. The registry's partial reporting supports a careful description of observed outcomes, but leaves important elements of the formal comparison unresolved.

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 does not report the specific events included in the primary SRE definition. Without that definition, readers cannot determine exactly which skeletal complications contribute to the primary endpoint or compare its scope with other studies. The primary population is described as eligible patients who completed treatment, but the record does not explain exclusions, missing outcome handling, or how this population relates to all randomized participants.

The non-inferiority margin and the sponsor's primary effect estimate and confidence interval are not reported. Although the sponsor analysis is identified as non-inferiority or equivalence and gives p <= .05, those missing details prevent independent assessment of the formal criterion. The record also flags a discrepancy with the simple unadjusted re-calculation but does not explain its source.

The results are pooled across metastatic breast cancer, metastatic prostate cancer, and multiple myeloma with bone involvement. The registry lists subgroup outcomes for breast and prostate cancer, but the available primary summary does not establish whether the pooled result is consistent across the cancer groups. The treatment period and primary follow-up are described up to 2 years; outcomes beyond that timeframe are not addressed by the posted primary result.

The registry reports no masking and does not give details about randomization procedures, allocation concealment, multiplicity control, interim analyses, or the original sample-size justification. Adverse-event denominators differ from the primary denominators without an explanation. These limitations concern the information available in the registry record; they do not establish that the corresponding procedures were absent from the study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Zoledronic Acid in Treating Patients With Metastatic Breast Cancer, Metastatic Prostate Cancer, or Multiple Myeloma With Bone Involvement — NCT00869206.
• Registry record last updated 2018-11-07; status last verified 2018-10.
• Results first posted 2018-11-07.
• 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

NCT00869206 is a completed randomized phase III parallel-group trial comparing zoledronic acid every 4 weeks with dosing every 12 weeks in metastatic breast cancer, metastatic prostate cancer, or multiple myeloma involving bone. The registry reports 1,822 enrolled participants and no masking. The primary outcome was the percentage with at least one SRE within 2 years after randomization, analyzed in eligible participants who completed treatment.

Posted primary percentages are 67.6% and 67.9%. The sponsor's reported Cochran-Mantel-Haenszel analysis is labeled non-inferiority or equivalence and reports p <= .05. A discrepancy is flagged between that analysis and an unadjusted re-calculation; the sponsor's own analysis takes precedence. The non-inferiority margin and sponsor effect estimate with interval are not reported in the registry record, limiting independent assessment of the formal conclusion.