Continued Efficacy and Safety of Zoledronic Acid (q 4 Wks vs. q 12 Wks) in the 2nd Year of Treatment in Patients With Bone Metastases From Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Continued Efficacy and Safety of Zoledronic Acid (q 4 Wks vs. q 12 Wks) in the 2nd Year of Treatment in Patients With Bone Metastases From Breast Cancer (NCT00320710), a randomized phase 3 study. The primary outcome is Proportion of Patients Who Experienced at Least One Skeletal Related Event (SRE).

2. Clinical Question

3. Trial Design

This was a prospective, randomized, double-blind, stratified, multicenter, parallel, two-arm phase 3 trial. It enrolled 416 participants and is listed as completed. The registry gives a start date of 2006-02 and a primary completion date of 2013-07. The trial examined continued treatment during the second year in people with breast cancer and bone metastases who had already received approximately 1 year of standard zoledronic acid treatment.

The primary comparison was between zoledronic acid every 4 weeks and zoledronic acid every 12 weeks. Participants in the less frequent schedule received placebo infusions at the intervening 4-week intervals to help preserve the double blind. The registry describes the study as stratified, but the stratification factors and their use in the analysis are not reported in the registry record.

A separate placebo / zoledronic acid arm appears in the intervention descriptions. It was later dropped, and participants assigned to it were switched to zoledronic acid every 4 weeks according to a study amendment. The primary outcome population is explicitly described as participants in the two zoledronic acid frequency groups. The registry does not report enough detail to reconstruct the full enrollment and follow-up history of the dropped arm or how its participants were handled in all analyses.

The primary outcome was the percentage of participants with at least one skeletal related event over 52 weeks. Secondary outcomes included time to first event, individual event types, pain and analgesic measures, bone markers and skeletal morbidity rate. Details of the original sample-size justification, analysis plan, interim analyses and handling of missing observations are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The population included participants who were in the zoledronic acid q4 weeks and zoledronic acid q12 weeks treatment groups.

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 Proportion of Patients Who Experienced at Least One Skeletal Related Event (SRE), measured over 52 weeks.

The primary endpoint measures whether a participant experienced at least one skeletal related event during the 52-week timeframe. The registry defines an event as a pathologic fracture, whether vertebral or non-vertebral, spinal cord compression, radiation to bone or surgery to bone. The endpoint is reported as a percentage of participants, so each person contributes to the result according to whether at least one qualifying event occurred; repeated events do not create additional participants in this particular measure.

This kind of endpoint is used to capture clinically consequential skeletal complications in a population with bone metastases. Its event definition combines several types of complications and interventions, so the overall proportion does not show which event type accounts for the result. Other registered outcomes separately address time to the first event, individual event types and skeletal morbidity rate. Those measures answer related but distinct questions.

The primary result applies to the two specified zoledronic acid groups, not to a comparison with an untreated control group. The registry reports 22.0% for every-4-weeks dosing and 23.2% for every-12-weeks dosing. These are observed proportions over the stated timeframe; they do not by themselves identify the causal effect with precision or establish equivalence. The record does not report additional details about event adjudication or the exact analysis procedures for this endpoint.

7. Results Posted in the Registry

• Zoledronic Acid q 12 Weeks: 23.2% (47/203) versus 22.0% (44/200) on control; risk difference 1.2 percentage points (95% CI -7.0 to 9.3), risk ratio 1.05 (0.73–1.51); unadjusted two-proportion z-test p = 0.782.

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.

Change From Baseline in Mean Composite Brief Pain Inventory (BPI) Score

• 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 deviations.
• Result:
  • Zoledronic Acid q 12 Weeks: mean 0.31 versus 0.24 on control; difference 0.07 (95% CI -0.51 to 0.65), standardized effect d = 0.03; z-test p = 0.813.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zoledronic Acid q 12 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Mean Analgesic Score

• 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 deviations.
• Result:
  • Zoledronic Acid q 12 Weeks: mean 0.50 versus 0.50 on control; difference 0.00 (95% CI -0.34 to 0.34), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zoledronic Acid q 12 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Urinary N-telopeptide / Creatinine Ratio

• 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 deviations.
• Result:
  • Zoledronic Acid q 12 Weeks: mean 14.70 versus 10.61 on control; difference 4.08 (95% CI -8.83 to 17.00), standardized effect d = 0.08; z-test p = 0.535.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zoledronic Acid q 12 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several dimensions of skeletal disease and treatment experience: time to first skeletal related event, individual event types, pain, analgesic use, bone markers and skeletal morbidity rate. Numerical summaries are posted for changes in BPI score, analgesic score and urinary N-telopeptide / creatinine ratio. The other listed outcomes broaden the clinical questions but do not have a numerical comparison described in the available summaries.

Across the numerical secondary measures, the posted group averages do not show a consistent, sharply separated pattern. The pain and bone-marker point estimates differ in one direction, while the analgesic averages are the same; their recalculated uncertainty intervals are broad enough to include no difference. This general pattern is compatible with the primary result’s lack of a clear separation, but the secondary outcomes measure different things and should not be treated as repetitions of the primary endpoint.

Secondary results can help assess whether a primary finding sits alongside changes in related measures, but they are usually less definitive when many outcomes are examined. The registry does not report sponsor analyses for the secondary outcomes, and the recalculations are unadjusted. When multiple outcomes are considered, the chance of seeing an apparently notable result by chance can increase. No multiplicity adjustment strategy is reported in the registry record.

These results therefore serve as supportive context rather than independent confirmation of a broad conclusion. A lack of an evident difference on a secondary measure is not evidence that the schedules have identical effects on that measure. Likewise, an isolated difference would require careful interpretation in light of uncertainty, the number of outcomes considered, and the absence of reported analysis procedures. The primary endpoint remains the main basis for interpreting the trial’s stated comparison.

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

• Time to First SRE
• Time to First Individual Type of SRE
• Change From Baseline in Mean Composite Brief Pain Inventory (BPI) Score
• Change From Baseline in Mean Analgesic Score
• Change From Baseline in Urinary N-telopeptide / Creatinine Ratio
• Change From Baseline in Serum Bone Specific Alkaline Phosphatase
• Skeletal Morbidity Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either experienced at least one qualifying skeletal related event during 52 weeks or did not. A proportion summarizes the fraction of each group with an event. It is an intuitive measure of how frequently the defined outcome occurred in the observed groups, but it does not preserve information about the number or timing of repeated events. The registry lists time to first event and skeletal morbidity rate as separate outcomes, which address different aspects of event experience.

What does the risk difference describe?

A risk difference compares the event proportions by subtraction, with the order of groups determining the sign. A value at zero corresponds to equal observed proportions; values on either side represent an observed difference in opposite directions. The unadjusted recalculation for this comparison uses the posted participant counts and event counts. Its confidence interval extends across zero, so the summary statistics are compatible with a range of possible differences, including no difference. The recalculated p-value is 0.782. It is an unadjusted comparison based on summary data, not a substitute for an analysis reported by the sponsor.

How should a p-value be understood?

In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value also does not capture the full range of estimates compatible with the data; that is one reason to consider the confidence interval alongside it. The registry does not report sponsor analyses for the primary outcome, so the posted p-value in this comparison is an unadjusted recalculation.

What does a confidence interval add?

In general, a confidence interval expresses uncertainty around an estimate under the assumptions of the method used. A broad interval means that the data do not pin down the comparison precisely. When an interval for a difference includes zero, the data are compatible with no difference as well as with differences in either direction. That does not establish equivalence. A formal equivalence or non-inferiority claim requires an appropriate design and margin, neither of which is reported in the registry record. The interval should be read as a range of uncertainty, not as a list of equally likely effects or a guarantee that the true effect lies inside it.

Why do analysis details matter?

The trial is described as randomized, stratified and double-blind, but the registry does not report which factors were used for stratification, how they entered the statistical model, or whether the primary analysis was adjusted. It also does not report the original statistical analysis plan, interim analyses, missing-data procedures, or a detailed definition of the analysis population beyond the two groups named for the primary endpoint. Those omissions prevent a full assessment of whether the posted summary statistics reflect all randomized participants, a particular follow-up population, or another analysis set.

Randomization helps make groups comparable on average, while blinding can reduce certain sources of differences in care or outcome assessment. These design features do not remove uncertainty from finite samples, missing observations, deviations from assigned treatment or outcome measurement. The registry supplies no details with which to assess those issues fully. The dropped placebo / zoledronic acid arm also makes it important not to assume that all 416 enrolled participants contributed to the main two-group comparison.

How do the secondary measures differ?

The secondary outcomes include both continuous measurements and event-based outcomes. For a continuous outcome, a group mean describes the average observed change, while the standard deviation describes variation among participants. A mean difference compares the two group averages. The pain, analgesic and urinary bone-marker entries report means and standard deviations, but the registry does not give sponsor-reported analyses for those outcomes. Their recalculated comparisons are based on posted summary statistics and are unadjusted.

For binary outcomes, comparing percentages is different from comparing means. For time-to-event outcomes, timing and censoring matter, and methods designed for event times are generally used. General statistical practice treats outcome type and analysis choices as linked: the method should reflect how the outcome is measured, how follow-up occurs and what question the study intends to answer. The registry’s original choices and assumptions for these analyses are not reported in the registry record.

The main statistical distinction is between a result that estimates an effect and the uncertainty around that estimate. The observed percentages, means and recalculated comparisons are descriptive evidence from this trial record. They should be interpreted with their uncertainty and with the limits of the reported analysis details, rather than as stand-alone proof of a treatment effect or its absence.

11. Confidence Intervals and Precision

The primary comparison has limited precision: the observed proportions are 22.0% and 23.2%, and the recalculated confidence interval for the risk difference includes zero. That interval also allows differences in either direction, rather than concentrating narrowly around no difference. The p-value of 0.782 is consistent with the lack of a clear statistical separation in this unadjusted comparison, but it does not show that the two schedules are equivalent.

Precision depends on the amount of information available, including the number of participants and events, as well as the variability of the outcome. The primary groups included 200 and 203 participants, and the event counts were 44 and 47. These counts provide the basis for the displayed proportions, but they do not eliminate uncertainty about the underlying comparison. A confidence interval is more informative about that uncertainty than a point estimate alone.

The posted secondary continuous outcomes also have uncertainty. For example, the BPI mean difference has a confidence interval spanning zero, while the analgesic score means are equal in the posted summaries. The urinary N-telopeptide / creatinine comparison has a confidence interval from -8.829 to 17.0. These results do not support a precise conclusion about a difference across all outcomes, particularly because their analyses are unadjusted and the registry gives no sponsor-reported analyses for these secondary measures.

Confidence intervals depend on analysis assumptions, and the registry does not report enough detail to evaluate every assumption used in the original study analyses. The intervals associated with the recalculations describe uncertainty under their own unadjusted methods. They should not be read as resolving uncertainty about missing observations, treatment changes or multiplicity. The central statistical message is therefore not simply that the observed group results are close, but that the available summaries leave meaningful uncertainty around the between-group effects.

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 translate the observed effects into hypothetical sample-size requirements under stated assumptions. For the primary binary endpoint, the figures are participants per arm. For continuous endpoints, they are also participants per arm. The registry’s assumption text distinguishes time-to-event planning, where figures would be total events, but the outcomes with planning illustrations in this record are not presented as time-to-event sample-size calculations.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect: 100%, 75% or 50%. The 80% power column describes the illustrative number of participants per arm under which a study would have an 80% chance of detecting the specified effect if the assumptions and effect were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are prospective planning quantities, not properties observed in the completed trial.

For the primary endpoint, the illustration gives 20,650 participants per arm for 80% power and 27,643 for 90% power when planning for 100% of the observed effect. The corresponding figures rise as the assumed target effect is reduced: planning for 75% or 50% of the observed effect requires more participants per arm. Smaller effects are harder to distinguish from random variation, so they generally require larger samples under otherwise similar assumptions.

These calculations are planning illustrations based on the observed effect, not observed power. They are not the trial’s original design calculations. The original sample-size justification and its assumptions are not reported in the registry record, and these illustrations should not be used to infer what the study was designed to detect.

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 = 0.220; treatment proportion p₁ = 0.232; average p̄ = 0.226.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5913 = 1.1588.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5912 = 0.4976.
4. n = (1.1588 + 0.4976)² / (0.0115)² = 20,649.1, rounded up to 20,650 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 <- 0.22                          # control proportion
p1 <- 0.231527093596059                          # 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(320710)
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 = 20,650 (80% power), 27,643 (90% power)
 75% of observed effect: n per arm = 36,544 (80% power), 48,922 (90% power)
 50% of observed effect: n per arm = 81,850 (80% power), 109,573 (90% power)
power.prop.test: 20649.1 
Simulated power at n = 20,650 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The study has one identified primary endpoint and a range of secondary outcomes. Considering many outcomes can raise the chance that at least one result appears unusual simply through random variation. Statistical methods can address this multiplicity, for example by controlling the overall error rate or by specifying a hierarchy of tests. Which approach, if any, was planned or used is not reported in the registry record.

The primary p-value in the posted comparison is an unadjusted recalculation. The record does not provide a sponsor-reported statistical analysis for the primary outcome or secondary outcomes, and it lists no analyses. Consequently, there is no basis in the record for determining whether the primary result was adjusted for stratification, whether secondary analyses followed a prespecified hierarchy, or how conclusions were intended to account for multiple testing. The unadjusted secondary comparisons should be treated as exploratory evidence rather than as a set of independent confirmatory findings.

Missing-data handling is also not reported in the registry record. The primary arm counts are 200 and 203, while the registry’s overall enrollment is 416. The available information does not explain all differences among those totals, the number randomized to each arm, or whether every randomized participant had complete primary outcome ascertainment. It also does not specify how participants with incomplete follow-up, treatment discontinuation or protocol deviations entered the analysis.

These omissions matter because missing observations can affect estimates if they are related to outcome risk or treatment assignment. General statistical methods make assumptions about missingness or use procedures to address it, but the relevant procedure and assumptions for this trial are not reported. The record also does not report an interim-analysis plan, stopping boundaries, or whether the analysis population was intention-to-treat or another defined population. No such features should be inferred from the randomized design alone.

The limitations do not invalidate the posted descriptive results. They do limit the ability to assess how closely those results follow the intended analysis plan and how robust they are to alternative handling choices. Conclusions should therefore stay close to the outcomes and group summaries recorded, with appropriate restraint about confirmatory interpretation.

15. 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: mucosal inflammation (7.7%), hypocalcaemia (7.7%), pathological fracture (7.7%), pleural effusion (7.7%), abdominal pain (2.5%).

The safety record reports serious adverse events among 50 of 198 participants at risk in the every-4-weeks group and 51 of 202 at risk in the every-12-weeks group. For other adverse events, the respective affected counts were 182 of 198 and 185 of 202. These figures describe participants recorded as affected; they are not event rates per person-time and do not indicate how many separate episodes each participant experienced.

Selected serious adverse-event terms include mucosal inflammation, hypocalcaemia, pathological fracture and pleural effusion, each listed as 7.7%. Abdominal pain and dyspnoea are each listed as 2.5%. The record also includes a placebo / zoledronic acid group with 3 serious-event participants among 13 at risk and 12 participants with other adverse events among 13 at risk. That arm was later dropped and participants were switched to the every-4-weeks schedule, so it is distinct from the primary two-arm comparison.

These entries should be read as descriptive safety reporting. They do not establish that treatment caused an adverse event or permit a full comparison of event timing or severity. Death counts are not reported in the registry record.

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

The primary result describes the proportion of participants with at least one defined skeletal related event during 52 weeks in two groups continuing zoledronic acid on different schedules after approximately 1 year of prior treatment. The observed proportions, 22.0% and 23.2%, are close. The unadjusted comparison does not give a clear statistical separation, and its interval includes no difference.

That finding does not prove the schedules are the same. A study can fail to identify a difference because the true effects are similar, because the estimate is imprecise, or for other reasons. Establishing equivalence or non-inferiority calls for a prespecified margin and suitable analysis; those details are not reported in the registry record. The observed comparison should not be translated into a claim that a clinically meaningful difference has been ruled out.

The result also does not compare zoledronic acid with no treatment. Both groups in the primary analysis received zoledronic acid; the assigned schedules differed in frequency. The trial’s findings should be interpreted within the population and treatment history described in the record, rather than automatically extended to other populations or treatment settings.

Secondary outcome summaries provide additional but limited context. The registry does not report sponsor analyses for those outcomes, and the recalculated comparisons are unadjusted. Safety entries describe affected participants and selected serious-event terms, but they do not establish causation. Missing-data handling, the original statistical plan and other analysis details are not reported.

In statistical terms, the posted evidence is compatible with a small observed difference and remains uncertain about the underlying contrast. It is not a definitive demonstration of no effect, equivalence, or a specific clinical advantage. The strongest interpretation is descriptive and bounded: the two primary group proportions were similar in the recorded 52-week comparison, with uncertainty that prevents a more conclusive statement.

17. Why This Trial Matters Statistically

This trial is statistically notable because it asks about treatment frequency after a period of prior therapy, rather than contrasting an active treatment with an untreated group. That distinction shapes what can be learned: the primary comparison concerns every-4-weeks versus every-12-weeks dosing among participants with the specified disease and treatment history.

The endpoint is a binary summary of a range of serious skeletal outcomes. It is straightforward to describe as a proportion, but the combined definition can conceal variation among fractures, spinal cord compression, radiation to bone and surgery to bone. The separate registered outcomes for time to first event, individual event types and skeletal morbidity rate illustrate why one endpoint may not capture every dimension of clinical experience.

The main comparison also illustrates the difference between a small observed contrast and a precise conclusion. The percentages are close, but the confidence interval includes values on both sides of no difference. A non-significant result is not the same as evidence of equivalence. This is an important distinction when readers encounter comparisons of treatment schedules and are tempted to treat a large p-value as proof that the options are identical.

The record further shows why statistical interpretation depends on reporting quality. The randomized, double-blind design is described, yet key details about analysis populations, missing observations, multiplicity and the original sample-size rationale are not reported. Without those details, the posted summaries can be interpreted, but the complete path from trial design to inferential conclusion cannot be reconstructed.

Finally, the planning illustrations make the observed effect size relevant to future study planning without converting the completed trial into a claim about observed power. They show that smaller targeted effects call for larger planned samples under the stated assumptions. The statistical lesson is to distinguish the estimated effect, its uncertainty, the design question and the reporting gaps.

18. 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 record leaves several trial-specific uncertainties. Although the study is described as randomized, stratified and double-blind, it does not identify the stratification factors or explain whether the primary comparison accounted for them. The original statistical analysis plan, sponsor-reported analyses and analysis population definition are not reported. As a result, the unadjusted recalculations should not be confused with a full reconstruction of the trial’s planned analysis.

Overall enrollment was 416, whereas the primary endpoint summaries include 200 and 203 participants in the two treatment groups. The record does not explain all participant flows or clarify the complete handling of the dropped placebo / zoledronic acid arm. It also does not describe missing outcome data, follow-up completeness, treatment discontinuations, protocol deviations or sensitivity analyses. These gaps make it difficult to judge whether the group summaries represent all randomized participants or a subset with available outcome measurements.

The outcome record includes a composite primary endpoint, with several clinically different event types combined into one participant-level measure. The posted percentage cannot show the contribution of each component. Although individual SRE outcomes are listed among secondary measures, the record does not supply numerical results for every listed outcome in the material summarized by the primary comparison. Event-adjudication details are not reported.

Secondary comparisons are unadjusted, and no multiplicity strategy is reported. Safety counts are descriptive, with no death counts reported. The original sample-size justification and interim-analysis plan are also not reported in the registry record. These limitations counsel against claims beyond the stated population, endpoints and posted summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Continued Efficacy and Safety of Zoledronic Acid (q 4 Wks vs. q 12 Wks) in the 2nd Year of Treatment in Patients With Bone Metastases From Breast Cancer — NCT00320710.
• Registry record last updated 2014-08-22; status last verified 2014-08.
• Results first posted 2014-08-04.
• 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.

22. Record Summary

NCT00320710 is a completed phase 3 randomized, double-blind, parallel trial in breast cancer patients with bone metastases who had received approximately 1 year of standard zoledronic acid treatment. The primary comparison was zoledronic acid every 4 weeks versus every 12 weeks during the second year. The primary endpoint was at least one skeletal related event over 52 weeks.

The posted primary proportions were 22.0% and 23.2%, with group sizes of 200 and 203. The unadjusted recalculation does not show a clear separation, but the uncertainty does not establish equivalence. Secondary outcomes cover pain, analgesic use, bone markers and skeletal events; their unadjusted results are limited. Important analysis, missing-data and multiplicity details are not reported in the registry record.