Evaluation of New or Worsening Lens Opacifications in Men With Non-metastatic Prostate Cancer Receiving Denosumab for Bone Loss: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of New or Worsening Lens Opacifications in Men With Non-metastatic Prostate Cancer Receiving Denosumab for Bone Loss (NCT00925600), a randomized phase 3 study. The primary outcome is Percentage of Participants With Lens Opacification Event Development or Progression by Month 12.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group study comparing denosumab with placebo. The registry lists quadruple masking and describes the study as double-blind and placebo-controlled. The record lists enrollment of 769 participants. The study status is completed; the recorded start date is 2009-11-30 and the primary completion date is 2016-05-12.

Participants assigned to denosumab received 60 mg by subcutaneous injection on Day 1 and at Month 6. Participants assigned to placebo received placebo by subcutaneous injection on the same schedule. The trial focused on men with non-metastatic prostate cancer receiving androgen-deprivation therapy, with the primary outcome addressing lens opacification in the context of denosumab use for bone loss.

The primary endpoint was assessed at 12 months. Its analysis population was defined by receipt of at least one dose and the availability of an evaluable baseline and at least one evaluable post-baseline LOCS III assessment at the corresponding lens site. This means the primary endpoint denominator need not represent everyone randomized. The record’s endpoint population description is incomplete and notes that three participants randomized to placebo received at least one dose of denosumab; the remaining details of that statement are not reported in the registry record.

The registry lists 7 outcome measures and 4 analyses. It does not report the trial’s original sample-size justification, its full statistical analysis plan, or whether interim analyses were conducted. These details should not be inferred from the final posted endpoint results or from illustrative sample-size calculations.

4. Participant Flow and Accounting

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

Before assignment: Participants were randomly assigned to receive denosumab or placebo in a 1:1 allocation ratio. Randomization was stratified on the basis of screening Lens Opacities Classification System (LOCS) III status (\< 3.0 at all sites versus ≥ 3.0 at any site); age group (\< 75, ≥ 75 years), and patient-reported history of cataract (yes/no).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The lens opacification analysis set includes randomized participants who received ≥1 dose of study drug, had an evaluable baseline and at least 1 evaluable post-baseline LOCS III assessment at the corresponding lens site. Three participants randomized to placebo who received ≥ 1 dose of denosumab in error are analyzed in the denosumab group.

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 Percentage of Participants With Lens Opacification Event Development or Progression by Month 12, measured over 12 months.

The primary endpoint was the percentage of participants with lens opacification event development or progression by month 12. The assessment used the Lens Opacities Classification System III (LOCS III), a slit-lamp-based grading method that uses photographs as references for grading different types of lens opacification. The categories described in the record are nuclear opalescence, nuclear color, cortical cataract, and posterior subcapsular cataract. Higher scores indicate greater severity.

An event was defined by a change from baseline of at least 1.0 in posterior subcapsular or cortical grading, or at least 0.7 in nuclear opalescence grading. The endpoint therefore converts changes in continuous grading scores into a binary outcome: each eligible participant is classified as having or not having development or progression according to the stated thresholds.

Using a binary endpoint makes it possible to report the proportion of participants meeting a clinically described grading-change criterion and compare those proportions between randomized groups. The threshold-based definition also makes the outcome more specific than simply recording any change in a grading score. However, the endpoint does not describe every possible change in lens grading, and a percentage alone does not show the size of score changes among participants who did meet the event definition.

7. Results Posted in the Registry

• Denosumab: 33.5% (127/379) versus 33.2% (124/374) on control; risk difference 0.4 percentage points (95% CI -6.4 to 7.1), risk ratio 1.01 (0.83–1.24); unadjusted two-proportion z-test p = 0.918.

8. Statistical Interpretation

9. Statistical Methods Explained

The endpoint is binary: each participant in the lens opacification analysis set either met the event definition by month 12 or did not. For a binary outcome, a group percentage expresses how common the event was among participants in that group. The posted percentages are 33.2 for placebo and 33.5 for denosumab. The posted counts are 124 of 374 and 127 of 379, respectively. The endpoint denominator is based on the analysis set described in the record, rather than automatically including every randomized participant.

What does a risk difference describe?

A risk difference compares the event proportions between two groups by subtracting one group’s proportion from the other’s. It is an absolute measure: it describes the gap between proportions on the outcome scale. The unadjusted recalculation reports a risk difference of 0.004. Its confidence interval runs from -0.064 to 0.071. Because this is a recalculation from posted summary counts, it does not include any adjustment that may have been used in the sponsor’s analysis.

Other common binary-outcome measures include a risk ratio and an odds ratio. A risk ratio compares proportions as a ratio; an odds ratio compares the odds of the event. The recalculated risk ratio is 1.011, with a confidence interval from 0.826 to 1.237. The recalculated odds ratio is 1.016, with a confidence interval from 0.750 to 1.376. These measures answer related but distinct questions, and their numerical scales are not directly interchangeable with the risk-difference scale.

What does a p-value tell the reader?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. The unadjusted recalculation has p = 0.918. The sponsor’s reported analysis has p = 0.003, but this is attached to a Mantel-Haenszel risk-difference analysis labelled non-inferiority or equivalence. Those p-values arise from different analyses and cannot be read as if they were competing calculations of an identical test.

For non-inferiority or equivalence, interpretation depends on a prespecified margin that defines what difference is acceptable for the stated purpose. The registry record does not report that margin or enough detail to assess how the sponsor’s test was specified. Consequently, the reported label and p-value should be described as posted, without inferring a threshold or treating the p-value alone as proof of equivalence.

Why can the analyses differ?

The sponsor reports a Mantel-Haenszel method, while the recalculation is a simple unadjusted comparison of the posted counts. General statistical methods can produce different estimates, intervals, or p-values when they use different adjustments, assumptions, analysis populations, or testing procedures. The registry record does not explain the specific source of this discrepancy. It is therefore not possible to attribute the disagreement to a particular adjustment or procedural choice. Since the discrepancy flag is true, the sponsor’s own analysis takes precedence.

Why does the analysis population matter?

Randomization establishes the assigned groups, but the primary endpoint analysis set was restricted to participants who received at least one dose and had evaluable lens assessments at baseline and after baseline. Such restrictions can make the analyzed population differ from the full randomized population. The record does not provide enough detail to reconstruct every participant’s inclusion, exclusion, or treatment classification. It also notes three participants randomized to placebo who received at least one dose of denosumab, but the related description is incomplete.

General statistical interpretation of a binary endpoint also depends on how missing assessments are handled. If participants without follow-up measurements are excluded, the reported percentage pertains to the evaluable analysis set, and its applicability depends in part on whether missingness is related to the outcome. The registry record does not report a missing-data method for this endpoint. It would be inappropriate to assume that missing outcomes were treated as events, non-events, or imputed values.

Finally, the registry lists multiple outcome measures and analyses. General statistical practice considers the risk of chance findings when many outcomes or tests are examined. The record does not report a multiplicity adjustment or a complete prespecified testing hierarchy, so the relationship between the reported analyses and any broader testing strategy is not reported in the registry record.

10. Confidence Intervals and Precision

The unadjusted recalculated risk difference is 0.004, with a confidence interval from -0.064 to 0.071. A confidence interval communicates uncertainty around an estimate: it gives a range of values compatible with the observed data under the method’s assumptions. It is not a guarantee that the true value lies in the interval, and it does not assign probabilities to individual values within it.

This interval extends across zero, so the recalculated data are compatible with a range that includes differences in either direction. Its width also means the recalculated estimate does not pin down the size of the group difference precisely. The confidence interval should be read alongside the estimate and the analysis method, rather than as a stand-alone verdict about whether the groups are the same.

The sponsor reports a different risk-difference estimate, 0.4, with a 95% confidence interval from -6.3 to 7.2. This interval likewise extends across zero on the sponsor’s reported scale. It belongs to the sponsor’s Mantel-Haenszel non-inferiority or equivalence analysis, not to the unadjusted recalculation. The registry record does not report the margin needed to assess the non-inferiority or equivalence interpretation.

Precision is also shaped by the analysis population and endpoint measurement. The primary endpoint included participants with evaluable lens assessments, and the registry description of that population is incomplete. The record does not report how missing endpoint assessments were handled. Thus, the intervals describe uncertainty under their respective analyses but cannot resolve concerns about missing-data handling or the disagreement between analyses.

11. Planning a Similar Trial: Sample Size

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

The planning estimates are illustrative calculations based on the observed effect, not the trial’s original design assumptions. They use 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 as the effect to detect. The listed estimates are participants per arm, not total participants. For this binary endpoint, the estimates are not counts of total events.

The 80% power column gives the estimated participants per arm under the stated assumptions for a design with 80% power to detect the chosen effect. The 90% power column gives the corresponding estimate for a design with 90% power. Power is a design property under assumed conditions: in general, it is the probability that a planned statistical test will detect an effect of the specified size if that effect is present and the assumptions hold.

The scenarios include planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The displayed participant requirements rise as the assumed effect becomes smaller. This is a general feature of study planning: smaller differences are harder to distinguish from random variation and therefore require more participants, all else being equal.

These calculations are not observed power and do not describe what the completed trial achieved. The original sample-size justification and design assumptions are not reported in the registry record. The estimates also rely on the observed effect, which is uncertain, and should be read as planning illustrations rather than as evidence about the adequacy of the original enrollment.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.332; treatment proportion p₁ = 0.335; average p̄ = 0.333.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6667 = 1.3066.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6667 = 0.5611.
4. n = (1.3066 + 0.5611)² / (0.0035)² = 278,118.5, rounded up to 278,119 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 <- 0.331550802139037                          # control proportion
p1 <- 0.33509234828496                          # 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(925600)
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 = 278,119 (80% power), 372,322 (90% power)
 75% of observed effect: n per arm = 494,105 (80% power), 661,466 (90% power)
 50% of observed effect: n per arm = 1,110,996 (80% power), 1,487,308 (90% power)
power.prop.test: 278118.5 
Simulated power at n = 278,119 per arm: 0.798 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor’s reported analysis is a Mantel-Haenszel risk-difference analysis, with an estimate of 0.4, a 95% confidence interval from -6.3 to 7.2, and p = 0.003. The registry labels it as a non-inferiority or equivalence analysis. The unadjusted recalculation from the posted group counts instead gives a risk difference of 0.004, a confidence interval from -0.064 to 0.071, and p = 0.918.

These results are not interchangeable: the sponsor’s method and the unadjusted recalculation are different analyses, and their reported results do not agree. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence. The recalculated result is useful as a transparent, simple comparison of the posted counts, but should not replace the reported sponsor analysis.

The registry record does not report the non-inferiority or equivalence margin, or sufficient detail to reconcile the discrepancy. The sponsor’s p-value should therefore be reported in the context of its labelled analysis, without treating it alone as evidence that the groups meet a particular equivalence threshold.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 7 outcome measures and 4 analyses. Multiple outcomes or statistical tests can increase the chance that at least one result appears notable by chance. General statistical approaches to this issue include prespecifying a hierarchy of tests or adjusting for multiple comparisons. The registry record does not report whether such an approach was used for these outcomes, so no adjustment or testing hierarchy should be assumed.

The primary outcome is identified as lens opacification event development or progression by month 12. The record does not provide a complete account of how the other listed outcome measures relate to the primary endpoint or to the sponsor’s non-inferiority or equivalence analysis. The extent to which the reported p-value reflects a prespecified analysis plan is not reported in the registry record.

The analysis population required at least one dose of study drug and evaluable baseline and post-baseline lens assessments. The record does not give complete participant-flow details for this endpoint, and the population description ends after noting that three participants randomized to placebo received at least one dose of denosumab. The reasons for any missing or unevaluable assessments, and their distribution by randomized group, are not reported in the registry record.

The registry record also does not report the method used to handle missing primary endpoint assessments. Without that information, it is not possible to determine whether missing outcomes were excluded, imputed, or addressed through another procedure. These choices can affect the analysis population and the interpretation of an endpoint percentage.

The record does not report whether interim analyses were performed, the original sample-size justification, or a full statistical analysis plan. Those details are relevant when assessing whether the final testing procedure followed a prespecified plan, but they should not be inferred from the posted outcome results.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebrovascular accident (1.1%), myocardial ischaemia (0.8%), coronary artery disease (0.5%), myocardial infarction (0.5%), diarrhoea (0.5%).

Serious adverse events were reported for groups with 380 participants at risk in the placebo group and 385 in the denosumab group. The registry reports 52 participants affected in the placebo group and 42 in the denosumab group. These figures describe participants with serious adverse events; they are not necessarily the number of distinct events, since one participant may experience more than one event.

For other adverse events, the groups at risk were 380 for placebo and 385 for denosumab. The registry reports 107 participants affected in the placebo group and 121 in the denosumab group. These are descriptive counts and do not by themselves establish that the groups differ because of treatment.

The listed serious adverse event terms include cerebrovascular accident at 1.1%, myocardial ischaemia at 0.8%, and coronary artery disease, myocardial infarction, diarrhoea, and diverticulitis at 0.5% each. These entries indicate reported terms and percentages; they do not establish causation or provide a complete safety profile. Death counts are not reported in the registry record. The safety figures should be interpreted separately from the primary lens-opacification endpoint.

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

The registry reports that 33.2 of participants in the placebo group and 33.5 of participants in the denosumab group met the LOCS III event-development or progression definition by month 12. Those percentages describe the endpoint and analysis population as recorded. They do not describe all lens changes, all participants randomized, or outcomes beyond the stated follow-up period.

The recalculated unadjusted comparison is imprecise and differs from the sponsor’s reported Mantel-Haenszel non-inferiority or equivalence analysis. The sponsor’s analysis takes precedence because the discrepancy flag is true, but the registry record does not report the margin needed to interpret the non-inferiority or equivalence label fully. The posted results therefore do not justify treating the two analyses as equivalent or drawing an unqualified conclusion from either p-value.

A close pair of percentages is not proof that two treatments have identical effects. Establishing equivalence or non-inferiority requires a defined margin and an analysis suited to that question. Conversely, an unadjusted p-value that is not small does not prove the absence of a difference. The confidence intervals communicate uncertainty and include values on either side of zero, but their interpretation remains tied to the respective analysis methods.

The findings also do not establish a general effect on cataracts or vision, since the endpoint is a specific threshold-based LOCS III measure at 12 months. Nor do the serious adverse event counts establish that any event was caused by study treatment. The registry record provides descriptive outcome and safety figures, but important analysis details—including missing-data handling and the non-inferiority or equivalence margin—are not reported.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it turns graded lens findings into a binary event using explicit LOCS III change thresholds. That approach creates an endpoint that can be compared as a percentage between randomized groups, while also making the result dependent on both the grading process and the selected threshold definition.

The posted group percentages are close, but the reported sponsor analysis and the unadjusted recalculation disagree. This illustrates why a numerical comparison should always be tied to its method, analysis population, and intended statistical question. A simple recalculation can help readers understand the posted counts, but it cannot substitute for a sponsor analysis that uses a different method, especially when a discrepancy is flagged.

The registry labels the sponsor’s analysis as non-inferiority or equivalence, yet does not report the margin required to assess that claim. This highlights an important general principle: a statistical label and p-value cannot be fully interpreted without the prespecified decision rule. Confidence intervals are also essential because they show the range of estimates compatible with an analysis, not merely whether a test crossed a threshold.

Finally, the evaluable-assessment analysis set and incomplete reporting of missing-data methods affect how broadly the endpoint percentages can be interpreted. The trial therefore offers a useful example of the distinction between posted descriptive results, an unadjusted recalculation, and the sponsor’s own inferential analysis.

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 primary endpoint analysis population required receipt of at least one dose and evaluable lens assessments at baseline and after baseline. The record’s description of that population is incomplete, so participant flow into the endpoint analysis cannot be fully reconstructed. It notes three participants randomized to placebo who received at least one dose of denosumab, but the remainder of the statement is not reported in the registry record.

The registry record does not report how missing or unevaluable lens assessments were handled, why they occurred, or whether the frequency differed between groups. Because the primary endpoint depends on follow-up grading, missing assessments could affect which participants contribute to the reported percentages. The record also does not report details about the reproducibility or blinding of LOCS III grading beyond the listed quadruple masking.

The sponsor’s reported Mantel-Haenszel estimate and the unadjusted recalculation differ. The reason for the discrepancy is not reported in the registry record. The sponsor’s analysis takes precedence, but the non-inferiority or equivalence margin and sufficient analysis details to assess that claim are not reported.

The record lists multiple outcome measures and analyses but does not report a multiplicity strategy, a full statistical analysis plan, interim analyses, or the original sample-size justification. The safety figures are descriptive, and death counts are not reported in the registry record. These reporting gaps limit assessment of the analysis choices and the scope of conclusions that can be drawn from the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of New or Worsening Lens Opacifications in Men With Non-metastatic Prostate Cancer Receiving Denosumab for Bone Loss — NCT00925600.
• Registry record last updated 2017-05-30; status last verified 2017-04.
• Results first posted 2017-05-30.
• 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

NCT00925600 is a completed phase 3 randomized, parallel-group, placebo-controlled study of denosumab for bone loss due to androgen-deprivation therapy in men with non-metastatic prostate cancer. The registry lists quadruple masking and enrollment of 769 participants. Denosumab 60 mg and placebo were administered by subcutaneous injection on Day 1 and at Month 6.

The primary outcome was lens opacification event development or progression by month 12, assessed using LOCS III grading thresholds. The posted percentages were 33.2 for placebo and 33.5 for denosumab. The sponsor reported a Mantel-Haenszel analysis labelled non-inferiority or equivalence; an unadjusted recalculation differs, and the sponsor’s analysis takes precedence. The registry record does not report the margin needed to evaluate that label fully or the method for handling missing endpoint assessments.