Efficacy and Safety of Letrozole vs. Letrozole Plus Zoledronic Acid as Endocrine Therapy Before Surgery in Postmenopausal Patients With Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Letrozole vs. Letrozole Plus Zoledronic Acid as Endocrine Therapy Before Surgery in Postmenopausal Patients With Breast Cancer (NCT00375752), a randomized phase 4 study. The primary outcome is Tumor Response Rate (Complete Response (CR) or Partial Response (PR)) Based on MRI- or Mammography and/or Sonography According to Modified RECIST Criteria at Month 6.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with enrollment of 168 and status recorded as terminated. It lists the phase as Phase 4. The official title calls the study a randomized open Phase II trial, while the registry’s design fields list quadruple masking. Those descriptions do not align; the registry record does not explain the difference. The reason for termination is not reported in the registry record.

The study evaluated preoperative endocrine treatment in postmenopausal patients with hormone-responsive breast cancer. One group received letrozole alone, and the other received letrozole with zoledronic acid. The official title specifies a 6 months treatment period; the arm descriptions specify approximately 6.5 months. Letrozole was described as oral treatment at 2.5 mg per day, and zoledronic acid as an intravenous dose of 4 mg every 4 weeks.

The primary endpoint was tumor response at month 6, assessed by MRI or mammography and/or sonography and classified according to modified RECIST criteria. The primary analysis population was modified intent-to-treat, requiring at least one post-baseline central assessment. The posted primary outcome group sizes are 66 for letrozole and 65 for the combination. These endpoint group sizes should not be confused with the safety group sizes, which differ.

The registry lists secondary outcomes covering central-review RECIST response, breast-conserving surgery, change in tumor size, and FACT-B total score. Change in tumor size is also available as a posted secondary result. A protocol-level description of the original sample-size assumptions, statistical plan, or reasons for the termination is 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 modified intent-to-treat (mITT) population included all patients of the ITT population for whom at least one post-baseline assessment of tumor response according to modified RECIST made by central review was available.

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 Tumor Response Rate (Complete Response (CR) or Partial Response (PR)) Based on MRI- or Mammography and/or Sonography According to Modified RECIST Criteria at Month 6, measured over 6 months.

The primary endpoint is the percentage of participants with a complete response or partial response at month 6, based on imaging reviewed centrally and classified using modified RECIST. The registry defines complete response as disappearance of all target lesions. Partial response requires a 30% decrease in the sum of the longest diameter of target lesions, using the baseline sum as the reference. The other RECIST categories are progressive disease and stable disease; neither is counted as a complete or partial response for this endpoint.

A response proportion is a binary outcome: each assessed participant either meets the complete-or-partial-response definition or does not. Summarizing the proportion gives a direct account of how often the prespecified response category was observed in each group. Central review can make outcome classification more consistent across participants, while imaging provides a way to assess tumor dimensions without relying only on subjective impressions.

That endpoint has limits. It captures response status at the stated assessment time, not how long a response lasts, whether surgery is possible, or later clinical outcomes. The registry lists separate secondary outcomes for breast-conserving surgery, tumor-size change, and FACT-B score, so those questions should not be treated as interchangeable with the primary response measure. The record also states that the primary analysis was underpowered because recruitment was insufficient, which makes the uncertainty around the observed response estimates particularly important.

7. Results Posted in the Registry

• Letrozole +Zoledronic Acid (LET+ZOL): 69.2% (45/65) versus 54.5% (36/66) on control; risk difference 14.7 percentage points (95% CI -1.8 to 31.1), risk ratio 1.27 (0.97–1.67); unadjusted two-proportion z-test p = 0.084.

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 Tumor Size (Longest Diameter) at Month 6

• 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:
  • Letrozole +Zoledronic Acid (LET+ZOL): mean -1.37 versus -1.12 on control; difference -0.25 (95% CI -0.57 to 0.07), standardized effect d = -0.27; z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Letrozole +Zoledronic Acid (LET+ZOL) and the control. The interval gives the range of effects that remain compatible with the data.

The registered secondary outcomes broaden the questions beyond the primary imaging-based response endpoint. They include central-review RECIST response, breast-conserving surgery, change in longest tumor diameter, and FACT-B total score. The available posted secondary comparison concerns change in tumor size. Results for the other listed secondary outcomes are not reported in the registry record in the registry record for this analysis.

The available tumor-size result is conceptually related to the primary response outcome because both concern tumor change during preoperative treatment. They are not interchangeable: one is a mean change in longest diameter, while the primary endpoint is the percentage meeting a categorical complete-or-partial-response definition. A difference in average size change does not automatically imply a difference in the proportion crossing the response thresholds, and the reverse is also true. The surgical and patient-reported outcomes address different aspects of the study question.

Secondary endpoints are useful for describing additional patterns, but they generally carry less confirmatory weight when many outcomes are examined. Testing multiple outcomes increases the chance that at least one result appears unusual by chance. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for these secondary tests, so their results should be treated as exploratory rather than as independent confirmation of the primary comparison.

The secondary results also have their own precision and analysis-population considerations. The tumor-size comparison has an unadjusted confidence interval that crosses zero, and its p-value is 0.128. Together with the underpowered primary analysis and the lack of posted results for other listed outcomes, the secondary evidence does not resolve the uncertainty in the primary response comparison.

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

• Best RECIST Response Based on Central Review at 6 Mos
• Number of Patients With Breast Conserving Surgery at 6 Months
• Change From Baseline in Tumor Size (Longest Diameter) at Month 6
• Mean Changes From Baseline in FACT-B Total Score at 6 Months (ITT, Data as Observed)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a response proportion represent?

For this primary outcome, response is classified as a binary event: a participant either has a complete or partial response under the modified RECIST definition, or does not. A group response proportion summarizes the fraction of assessed participants meeting that definition. Comparing proportions focuses on the frequency of the event, rather than on the amount of tumor shrinkage among responders alone. The endpoint description says baseline sum of longest diameter was the reference for determining objective response.

The posted outcome is based on a modified intent-to-treat population, defined as members of the intent-to-treat population with at least one post-baseline tumor-response assessment made by central review. That population definition matters: patients without an available post-baseline central assessment are not included in the described primary population. The record does not report a detailed missing-data method for patients without such an assessment.

What does the risk difference describe?

A risk difference subtracts the event proportion in the comparison group from the event proportion in the treatment group. It is expressed on the probability scale, so zero represents equal proportions, positive values indicate a higher event proportion in the treatment group, and negative values indicate a lower one. The recalculated risk difference is 0.147 for letrozole plus zoledronic acid compared with letrozole alone. Its 95% confidence interval is -0.018 to 0.311. Because zero lies within that interval, the summary estimates are compatible with no difference as well as with effects in either direction within the interval.

This is an unadjusted comparison of the posted group summaries. It does not account for any covariates or other analysis choices not described in the available result. The record’s reported test is Fisher Exact, but the recalculated risk difference and its interval are not a replacement for an analysis specified in the trial’s original protocol.

What do the p-values tell us?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not measure the probability that a result will replicate. The recalculated unadjusted p-value is 0.084; the registry reports p = 0.106 for its Fisher Exact analysis. Neither value should be treated as a measure of clinical importance. The estimates and their confidence intervals provide information about direction and precision that a p-value alone cannot convey.

A p-value above a conventional threshold does not prove the treatments have equal response proportions. That distinction is especially relevant because the registry states that the primary analysis was underpowered due to insufficient recruitment. The absence of a statistically conclusive result can reflect imprecision; it should not be recast as evidence of equivalence.

Why can a confidence interval be more useful than a threshold?

A confidence interval describes the range of effect estimates that are reasonably compatible with the observed data under the method used. In repeated use of the same procedure under its assumptions, intervals at the stated confidence level would cover the underlying parameter at that frequency. For an individual trial, the interval is best read as an uncertainty range, not as a guarantee that the true effect lies inside it. Here, the risk-difference interval crosses zero and extends to positive values, so it conveys both the uncertainty about direction and the uncertainty about magnitude.

Why do analysis populations matter?

The primary analysis population is not simply described as everyone enrolled. It requires membership in the intent-to-treat population and at least one post-baseline central response assessment. The posted group sizes for the primary endpoint are 66 and 65. Safety results use separate groups of 79 and 89. Different populations can arise because outcomes have different analysis requirements, but the record does not give a participant flow account that explains the differences. It also does not report a missing-data imputation approach for the primary endpoint.

The modified population definition can affect interpretation if assessment availability is related to treatment assignment or response. Without details on the reasons for missing assessments and the handling of missing data, the direction or extent of any such effect cannot be determined from the registry record.

What does the continuous secondary result measure?

The tumor-size secondary outcome is the mean change from baseline in longest diameter at month 6, measured in centimeters. Negative changes indicate a decrease from baseline under the reported change measure. The record provides group means and standard deviations, as well as a recalculated mean difference and confidence interval. A mean difference summarizes the separation between group averages, while the standard deviation describes variation among individual observations within a group. These quantities answer a different question from the binary response proportion: they describe average change in a measured dimension rather than the proportion meeting a response category.

Standard deviations should not be confused with standard errors. A standard deviation describes spread among observations; a standard error describes uncertainty in an estimated mean. The posted secondary results report standard deviations for the group changes, and separate standard errors are available in the comparison details. Statistical interpretation should preserve that distinction.

Why do planning illustrations depend on effect size?

Sample-size planning asks how many participants would be needed under a specified design and set of assumptions to detect an effect of a chosen size with a chosen probability. Smaller effects are harder to distinguish from random variation, so planning for a smaller effect generally requires more participants. The planning illustrations use fractions of the observed effect and stated assumptions, rather than reconstructing the original study design. They are not evidence about the probability that this completed trial detected an effect.

For binary outcomes, the calculation also depends on the event proportion and the chosen comparison method. For continuous outcomes, it depends on the scale of the effect and variability. These are general statistical principles; the registry record does not report the original sample-size justification or the trial’s own prespecified power assumptions.

11. Confidence Intervals and Precision

The primary response estimates are accompanied by 95% confidence intervals: 41.8% to 66.9% for letrozole and 56.6% to 80.1% for letrozole plus zoledronic acid. Each interval spans a substantial range of possible response proportions, indicating that the group estimates are not highly precise. The intervals also overlap, although overlap between separate group intervals is not itself the formal test of the difference between groups.

The recalculated risk-difference interval, -0.018 to 0.311, is the direct interval for the unadjusted group contrast. It includes zero and ranges from a small difference in one direction to a larger difference in the other. This means the data do not pin down either the direction or size of the difference with high precision. The point estimate of 0.147 should therefore be considered alongside the interval, not read as a definitive estimate of the effect.

The registry’s primary outcome description states that the analysis was underpowered because of insufficient recruitment. Limited recruitment can leave fewer observations contributing to an endpoint and produce wider uncertainty, though the record does not give the original target enrollment or a sample-size justification. The primary analysis population and safety populations also differ, so the precision of the response estimates should not be inferred from the safety group sizes.

Confidence intervals do not account for every possible source of uncertainty. They do not resolve concerns about missing response assessments, choice of analysis population, or whether the endpoint captures outcomes important beyond the imaging assessment. The registry record does not report enough detail to quantify those issues.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations, not a report of the trial’s original design. For these outcomes, the figures are participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations use the observed effect or a stated fraction of it as the effect to detect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned participants per arm for a design that would have an 80% chance of detecting the selected effect under the stated assumptions, if that effect were the true effect and the assumptions held. The 90% power column describes the corresponding planning target with a higher chance of detection. These columns do not report the power achieved by the completed trial. The illustrations are not observed power.

Rows for 100% of the observed effect use the observed effect size as the planning target. Rows for 75% and 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so the planning figures rise as the target effect gets smaller. For example, planning for 75% of the observed effect gives 310 participants per arm for 80% power and 414 participants per arm for 90% power. Planning for 50% of the observed effect gives 708 participants per arm for 80% power and 947 participants per arm for 90% power.

The curve should be read as a visual companion to those planning values: it illustrates how the required per-arm enrollment changes with the effect size under the listed assumptions. It does not show a trial result, and it does not establish that a future study would have the same effect or variability. The calculations are illustrative rather than a retrospective judgment about whether the terminated trial could have reached a conclusive result.

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 = 0.545; treatment proportion p₁ = 0.692; average p̄ = 0.619.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6868 = 1.3462.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6789 = 0.5714.
4. n = (1.3462 + 0.5714)² / (0.1469)² = 170.5, rounded up to 171 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 <- 0.545454545454545                          # control proportion
p1 <- 0.692307692307692                          # 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(375752)
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 = 171 (80% power), 228 (90% power)
 75% of observed effect: n per arm = 310 (80% power), 414 (90% power)
 50% of observed effect: n per arm = 708 (80% power), 947 (90% power)
power.prop.test: 170.5 
Simulated power at n = 171 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 reports a Fisher Exact analysis for the comparison and labels its parameter as an odds ratio. The reported value is 14.7, with a 95% confidence interval from -1.8 to 31.1 and p = 0.106. The recalculated analysis instead presents an unadjusted risk difference of 0.147, with a 95% confidence interval from -0.018 to 0.311 and p = 0.084. The registry record does not flag a discrepancy between its analysis and the recalculation.

These results should not be treated as identical estimates: an odds ratio and a risk difference use different scales and describe the contrast differently. The registry’s reported value and interval are reproduced as recorded, rather than converted or relabeled. The recalculated result is a simple unadjusted calculation from the posted summary statistics; it does not replace the sponsor’s reported analysis or imply that the trial used the recalculated method.

Both analyses leave uncertainty about the comparison. The sponsor-reported p-value is 0.106, and the recalculated p-value is 0.084. A difference between p-values does not by itself establish a contradiction, particularly when the reported parameterization and calculation differ. The registry record does not provide enough detail to determine all analytic choices behind the sponsor’s result beyond identifying Fisher Exact and the odds-ratio parameter. The study’s stated underpowered status also counsels against interpreting either result as proof of equivalence or as a definitive treatment effect.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary response endpoint and several secondary outcomes. When a study evaluates multiple outcomes or makes multiple comparisons, the chance of at least one apparently positive finding by chance can increase. Statistical methods can address that issue through adjustments or a prespecified testing hierarchy. Such an approach is not reported in the registry record. The unadjusted secondary results should therefore be read as descriptive evidence, not as a collection of independent confirmatory tests.

The primary population is modified intent-to-treat and requires at least one post-baseline central tumor-response assessment. This definition excludes members of the intent-to-treat population without an available qualifying assessment, but the record does not describe how many assessments were missing, why they were missing, or how missing outcomes were handled. Those details matter because missingness can affect estimates if it is related to treatment assignment or response. No imputation strategy or sensitivity analysis is reported in the registry record.

The posted primary response groups contain 66 and 65 participants, while the safety groups contain 79 and 89. These are distinct analysis populations for different outcomes; the record does not provide a participant-flow explanation for the differences. It would be inappropriate to assume that a missing response assessment means treatment discontinuation, or to infer the reasons for the different group sizes.

The record states that the primary analysis was underpowered because of insufficient recruitment. It does not report the original sample-size justification, planned target for the primary population, interim analyses, or a detailed statistical analysis plan. The reason for trial termination is also not reported in the registry record. Without those details, it is not possible to assess whether the posted analyses followed a prespecified plan or to determine the intended handling of multiple outcomes and incomplete data.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fall (4.5%), general physical health deterioration (3.4%), thrombocytopenia (1.3%), appendicitis perforated (1.3%), arthralgia (1.3%).

The safety results use groups of 79 participants assigned to letrozole and 89 assigned to letrozole plus zoledronic acid. Serious adverse events affected 3 participants in the letrozole group and 14 in the combination group. Other adverse events affected 56 and 67 participants, respectively. These counts use the safety populations and should not be conflated with the smaller groups used for the primary response analysis.

The listed serious adverse-event terms include fall at 4.5%, general physical health deterioration at 3.4%, and thrombocytopenia, perforated appendicitis, arthralgia, and osteochondrosis at 1.3% each. These are registry-listed terms and percentages; the record does not provide enough detail in this summary to establish whether a participant could contribute to more than one term or how events were attributed to treatment.

Deaths are not reported in the registry record. The available counts describe reported events in this trial and do not, by themselves, establish a causal relationship to either treatment. They also do not provide a complete comparison of all possible harms, event timing, severity, or exposure-adjusted rates. Safety interpretation should therefore remain descriptive and separate from conclusions about tumor response.

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

The primary result shows that the observed month-6 complete-or-partial-response proportion was higher in the letrozole-plus-zoledronic-acid group than in the letrozole group. The recalculated risk-difference point estimate is positive, but its confidence interval includes zero. The evidence therefore does not give a precise estimate of the difference or establish that the true response proportions differ. The registry itself notes that the primary analysis was underpowered because recruitment was insufficient.

This is not evidence that the two regimens are equivalent. Demonstrating equivalence or non-inferiority requires a specific design, margin, and analysis; those are not reported in the registry record. Nor should the point estimate alone be taken as proof that adding zoledronic acid changes response. The data are compatible with a range of possible differences, including no difference.

The outcome is a radiographic response category assessed at month 6. It does not establish how long any response lasts, what happens after surgery, or whether patient-reported quality of life differs. Those questions require their own outcome data. Although the registry lists breast-conserving surgery and FACT-B outcomes, results for those listed endpoints are not reported in the registry record in the registry entries.

The safety counts are descriptive and use a different analysis population from the primary endpoint. They do not by themselves demonstrate that one regimen is safer or less safe. A full benefit-harm judgment would require complete outcome reporting, suitable comparisons, and attention to event attribution and follow-up, details that are not available in the registry record.

Overall, the posted findings are best read as an imprecise comparison in a trial whose primary analysis was described as underpowered. They inform what was observed among the analyzed participants but do not support a definitive claim about efficacy, equivalence, or safety.

18. Why This Trial Matters Statistically

This trial illustrates why effect estimates and uncertainty intervals should be read together. The observed response proportions differ, and the recalculated point estimate favors the combination on the response scale. Yet the interval for the risk difference includes zero and spans a wide range. A reader who focuses only on the direction of the point estimate could overstate what the data establish; a reader who focuses only on whether a p-value crosses a threshold could overlook the range of effects still compatible with the results.

It also shows how outcome populations affect interpretation. The primary response analysis requires a post-baseline central assessment, whereas the safety results use different group sizes. Without participant-flow details, those denominators cannot be treated as interchangeable. Clear reporting of analysis populations and missing assessments is essential for judging how well a result represents the randomized groups.

The study’s registry description makes the power limitation explicit: the primary analysis was underpowered due to insufficient recruitment. Planning illustrations based on observed effects can help readers understand how effect size and desired power relate to enrollment, but they cannot recover the original design assumptions or the result that a differently sized study would have produced. The original sample-size justification is not reported in the registry record.

Finally, the record demonstrates the value of distinguishing a trial-reported analysis from a transparent recalculation. The registry reports a Fisher Exact result labeled as an odds ratio, while a simple unadjusted re-calculation expresses the comparison as a risk difference. Keeping those measures distinct prevents an apparent numerical mismatch from being mistaken for a direct contradiction and makes the estimand clear.

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.

Recruitment is a central limitation: the registry states that the primary analysis was underpowered because of insufficient recruitment. The record also marks the study as terminated, but the reason for termination is not reported in the registry record. The original enrollment target, sample-size justification, and any changes to the recruitment plan are not reported, so the extent to which the completed enrollment differed from the original plan cannot be assessed.

The primary analysis includes only patients with at least one post-baseline central response assessment. The registry does not provide a participant-flow account, reasons for unavailable assessments, or a missing-data analysis. This leaves uncertainty about how the analyzed population relates to the randomized groups. The primary response group sizes and safety group sizes differ, and no explanation for that difference is reported.

The registry’s design descriptions are not fully aligned: the official title calls the trial open Phase II, while the design fields list Phase 4 and quadruple masking. The record does not explain the differing descriptions. This limits the ability to interpret exactly how masking was implemented from the registry summary alone.

Additional limitations include the short, specified month-6 primary assessment and the lack of reported results for several listed secondary endpoints. The record does not report an adjustment for multiple outcomes, a detailed statistical analysis plan, or interim analyses. Serious adverse-event counts are descriptive, deaths are not reported in the registry record, and the available summary does not establish causal attribution. These constraints make the findings informative but not definitive.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Letrozole vs. Letrozole Plus Zoledronic Acid as Endocrine Therapy Before Surgery in Postmenopausal Patients With Breast Cancer — NCT00375752.
• Registry record last updated 2017-06-26; status last verified 2017-06.
• Results first posted 2012-04-25.
• 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

NCT00375752 is a terminated randomized parallel-group trial of preoperative letrozole, with or without zoledronic acid, in postmenopausal patients with hormone-responsive breast cancer. The registry lists Phase 4, quadruple masking, and enrollment of 168, while the official title describes a randomized open Phase II trial. The reason for termination is not reported in the registry record.

The primary outcome was complete or partial tumor response at month 6 by central review using modified RECIST. The posted response proportions were 54.5% with letrozole and 69.2% with the combination. The recalculated unadjusted risk difference was 0.147, with a 95% confidence interval from -0.018 to 0.311. The registry states that the primary analysis was underpowered because of insufficient recruitment.

Secondary outcomes included surgery, tumor-size change, and FACT-B score. Safety results report serious and other adverse-event counts in separate groups. The registry record does not report the original sample-size justification, detailed missing-data methods, multiplicity handling, or the reason for termination.