A Study of Bonviva (Ibandronate) Once Monthly in Post-Menopausal Women With Osteopenia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Bonviva (Ibandronate) Once Monthly in Post-Menopausal Women With Osteopenia (NCT00129623), a randomized phase 4 study. The primary outcome is Relative Change From Baseline in Mean Bone Mineral Density (BMD) of the Lumbar Spine (L2 to L4) at Month 12.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, double-blind, parallel-group, placebo-controlled, multicenter study sponsored by Hoffmann-La Roche. It studied oral ibandronate once monthly in postmenopausal women with osteopenia. The registry describes a two-arm comparison: monthly ibandronate 150 mg or monthly placebo. The registered enrollment was 160. The study started in 2005-12, had primary completion in 2007-12, and is recorded as completed.

Random allocation and double masking are stated in the registry record, but further operational details are not reported. For example, the record does not describe the randomization sequence, allocation concealment, the people covered by masking, or the procedures used to preserve masking. The registry also does not report the planned treatment duration in a more precise form than the brief study description’s anticipated range of 1-2 years. It does not report whether actual treatment duration differed from that expectation.

The primary outcome was evaluated at baseline and Month 12. The primary analysis population was not simply described as everyone enrolled: it included randomized participants who received at least one dose and had baseline and at least one follow-up evaluation. The endpoint results list 70 participants for placebo and 68 for ibandronate. The registry record does not give a participant-flow account explaining how people moved from enrollment to the endpoint analysis or why any participants were not included in those counts.

The listed design features support a between-group comparison, but the record does not report the trial’s original sample-size justification, its intended statistical analysis plan, or whether interim analyses were planned. Those omissions matter when interpreting how the study was planned and whether the reported analysis corresponds to every prespecified decision. The reported primary analysis is an ANOVA comparison of mean difference, and its estimate is close to the simple unadjusted recalculation from the posted group summaries.

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: Of the 451 participants who were screened, 160 participants were randomly assigned to the two treatment arms (Placebo and Ibandronate). The major reason for screening failure was participants did not meet the Bone Mineral Density (BMD) entry criteria.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population included participants who were randomized, received at least one dose of the trial medication and had baseline and at least one follow-up evaluation data point.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Baseline characteristics are presented for the safety population which included participants who had at least one dose of the trial medication documented in the case report form (CRF) whether withdrawn prematurely or not.

6. Primary Endpoint

The registry lists the primary outcome as Relative Change From Baseline in Mean Bone Mineral Density (BMD) of the Lumbar Spine (L2 to L4) at Month 12, measured over Baseline and Month 12.

The primary endpoint was relative change from baseline in mean bone mineral density of the lumbar spine, measured across L2 to L4, at Month 12. Bone mineral density was measured using a single dual-energy x-ray absorptiometry scan at screening and again at Month 12. The endpoint expressed the change as a relative difference between the baseline value and the last individual measurement available at 12 months, scaled as a percentage. The registry record states the formula as 100 multiplied by the difference between the one-year and baseline measurements, divided by the baseline measurement.

This endpoint represents a continuous measurement. A continuous outcome retains information about the amount of change rather than reducing each participant to a binary category such as responder or nonresponder. Comparing group means can therefore describe the average difference in measured bone density over the stated interval. The mean difference between groups is the main contrast for interpreting the result; the group-specific means describe the direction and scale of the changes.

DEXA measurement is relevant because the endpoint is a quantitative measure of bone mineral density. The record specifies that a measurement could be unsuitable if there was a fracture, an osteoarthritic process, or a scanning artifact that could not be removed sufficiently to preserve accurate measurement, as judged by the central reading center. The record does not describe how many measurements were deemed unsuitable or how such cases were handled in the analysis. The endpoint therefore needs to be read together with the stated analysis population and the missing-data details, which are not fully reported.

7. Results Posted in the Registry

• Ibandronate (IBN) 150 mg Monthly: mean 3.73 versus -0.39 on control; difference 4.12 (95% CI 2.96 to 5.28), standardized effect d = 1.19; z-test p = <0.001.

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.

Absolute Change From Baseline in Mean Lumbar Spine BMD at Month 12

• 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:
  • Ibandronate (IBN) 150 mg Monthly: mean 0.03 versus -0.00 on control; difference 0.04 (95% CI 0.03 to 0.05), standardized effect d = 1.14; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ibandronate (IBN) 150 mg Monthly than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes spanning absolute and relative bone mineral density changes, serum CTX changes, responder status, adverse events, serious adverse events, and marked laboratory abnormalities. Together, these outcomes cover related bone measurements as well as safety and response classifications. The listed endpoint domains indicate that the study was not restricted to the primary relative lumbar spine measure.

The posted secondary results include an absolute-change comparison for mean lumbar spine bone mineral density at Month 12. Its direction is consistent with the primary result: the group contrast favors a greater average increase in the ibandronate arm on the reported scale. This provides a related view of the lumbar spine result, since the primary endpoint expresses change relatively while the secondary endpoint expresses absolute change. It should not be treated as an independent replication, because both outcomes come from the same trial and related measurements.

The remaining secondary outcomes are named in the registry, but their numerical results are not reported in the registry record in the registry record for interpretation. It is therefore not possible to characterize a complete pattern across proximal femur outcomes, serum CTX, responder status, or laboratory abnormalities. The presence of an outcome in the registry does not establish the direction or size of its result.

Secondary results generally carry less inferential weight than a prespecified primary result, especially when the record does not describe a multiplicity strategy. Testing several outcomes can increase the chance of at least one apparently unusual finding if each is interpreted without adjustment. The registry does not report whether secondary tests were adjusted, ordered hierarchically, or designated as exploratory. Their interpretation should therefore remain supportive and cautious, with emphasis on the primary endpoint and on whether the total set of results is fully reported.

The secondary endpoint listing also includes adverse-event and laboratory outcomes, but these are not substitutes for a comprehensive safety assessment. Event counts, definitions, follow-up, exposure, and attribution all affect interpretation. The registry contains some adverse-event summaries, but does not report enough detail to establish a complete comparative safety profile from the listed secondary outcome names alone.

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

• Absolute Change From Baseline in Mean Lumbar Spine BMD at Month 12
• Relative Change From Baseline in Mean Proximal Femur BMD at Month 12
• Absolute Change From Baseline in BMD of the Proximal Femur at Month 12
• Relative Change From Baseline in Serum C-telopeptide Crosslinks of Type 1 Collagen (CTX)
• Absolute Change From Baseline in sCTX
• Percentage of Responders
• Number of Participants With Any Adverse Events (AEs) and Serious Adverse Events (SAEs)
• Number of Participants With Marked Laboratory Abnormalities

9. Statistical Interpretation

10. Statistical Methods Explained

Understanding the result starts with the form of the endpoint. Relative change in lumbar spine bone mineral density is continuous, meaning that each participant contributes a measured value on a numerical scale rather than only a category. A group mean summarizes the average value in that group. The mean difference compares the average outcome in the ibandronate group with the average outcome in the placebo group. A positive difference in this comparison indicates a higher average relative change in the ibandronate group, given the ordering used in the posted comparison.

What does the confidence interval describe?

A confidence interval describes the uncertainty around an estimated effect under the statistical model and sampling process. It gives a range of values compatible with the observed data and the method’s assumptions, rather than a guarantee that the true effect lies within that particular interval. A narrower interval indicates greater precision; a wider interval indicates less precision. The primary interval extends from 2.962 to 5.284 percentage points. Because the interval is above zero, the posted result is consistent with a positive between-group mean difference under the reported analysis. The interval does not account for every possible source of uncertainty, such as bias from missing observations or limitations in measurement.

What does the p-value add?

A p-value describes how unusual results at least as incompatible with the null hypothesis would be if the null hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, nor is it the probability that the result happened “by chance.” The registry’s reported analysis gives p < 0.001, while the unadjusted recalculation gives p < 0.001. These values should be read alongside the estimated difference and its confidence interval. The estimated size and precision describe the contrast more directly than a p-value alone.

The registry reports an ANOVA analysis with a mean-difference parameter and a 95% confidence interval. ANOVA is a method for comparing group means. In a two-group setting, it assesses whether the observed mean contrast is compatible with a null difference, given the analysis model. The registry does not describe the ANOVA specification beyond identifying the method and reported contrast. It is not reported in the registry record whether covariates were included, what assumptions were checked, whether there were transformations, or how any deviations from model assumptions were addressed. No more detailed reconstruction of the sponsor’s model is justified from the record.

How does the recalculation differ?

The recalculated comparison uses the posted group summaries to form a simple, unadjusted estimate of the difference and its uncertainty. It is useful as a check on the scale and direction of the sponsor-reported result. The recalculated mean difference and confidence limits closely match the sponsor’s reported values. The recalculation does not reproduce an undocumented analysis plan, account for participant-level data, or test whether the sponsor’s model choices were appropriate. It is a summary-statistic comparison, not a substitute for the reported analysis.

The posted group summaries include standard errors for the primary means, while the recalculation uses an approximate pooled standard deviation. A standard error describes the uncertainty of a sample mean, whereas a standard deviation describes spread among individual measurements. These quantities answer different questions. Recovering an approximate standard deviation from a standard error depends on the group sample size and the relationship between the reported statistic and the underlying observations. As a result, a recalculation based on summary statistics may be less exact than an analysis of participant-level data. The record marks the pooled standard deviation for the primary endpoint as approximate.

Why does variability matter?

General statistical explanation: variability describes how much individual observations differ from one another. Greater variability makes it harder to distinguish a group contrast from the background spread in outcomes, all else being equal. If outcomes are more variable than a simple model assumes, the estimated uncertainty can be too small, which may make confidence intervals overly narrow and p-values overly small. This is one reason model assumptions and diagnostics matter. The registry does not report a formal assessment of variability assumptions or over-dispersion for this endpoint, so no conclusion about those checks can be drawn.

The study’s randomization and masking are design features intended to support a fair comparison, but they do not eliminate all potential bias or uncertainty. The record states that the study was randomized and double-blind, but does not provide details about allocation concealment, the people masked, or the success of masking. Nor does it give a detailed account of protocol deviations, adherence, or measurement exclusions. The interpretation of a statistical model depends both on its calculations and on how the data were generated and selected for analysis.

What is not established by a significant result?

A small p-value does not establish clinical importance, measurement validity, generalizability, or the absence of bias. Statistical significance refers to evidence against a specified null hypothesis under a particular model. It does not show that all registered outcomes were positive, that every participant had a similar response, or that the estimate would be the same in other populations or settings. The record does not report a minimal clinically important difference or a prespecified threshold for interpreting the magnitude of the primary result. The statistical evidence should therefore be kept separate from claims about clinical value.

Multiple outcomes create another interpretive issue. The registry lists a primary endpoint and several secondary outcomes. If many hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis plan controls that risk. The record does not report whether secondary comparisons were adjusted for multiplicity, whether outcomes were hierarchically ordered, or whether any testing procedure was prespecified. The primary result has a distinct status because it is designated as primary, but the details of the study’s complete testing strategy are not reported.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 4.123 percentage points, with a 95% confidence interval from 2.962 to 5.284. The interval gives a sense of precision around the estimated group contrast: values within that range are compatible with the data under the reported analysis and its assumptions. Its placement entirely above zero supports a positive average difference in the analyzed sample. The interval is not a range containing every participant’s response, and it does not show how widely individual outcomes were distributed.

Precision should be judged from the interval as well as the p-value. A small p-value can occur with a precise estimate, but it does not explain the estimate’s scale or its plausible range. The interval communicates that the statistical analysis is not equally compatible with a zero difference and with every possible effect size; rather, it concentrates the compatible values within the stated bounds. The record does not supply a threshold for clinical importance, so the interval cannot by itself distinguish effects that are clinically important from those that are not.

The interval is based on the reported analysis, and its interpretation depends on the model and data being suitable for that analysis. The registry identifies ANOVA but does not report detailed model assumptions, diagnostic checks, or handling of missing outcome data. Thus, the interval quantifies sampling uncertainty under the analysis, not uncertainty from every possible source. In particular, it does not automatically account for selection that could arise if participants without follow-up measurements differ systematically from those analyzed.

The recalculated interval is close to the sponsor-reported interval. That agreement supports the numerical consistency of the posted summary comparison with the sponsor’s stated estimate, but does not verify undocumented model decisions or data handling. The primary endpoint groups contain 70 and 68 participants, respectively; those analysis counts help contextualize the estimate but do not resolve the missing-data questions. The registry does not report how many otherwise eligible participants lacked a Month 12 measurement, how unsuitable scans were distributed, or whether imputation was used.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for a continuous-outcome comparison; they are not total event counts. The illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect used for each planning scenario is a stated fraction of the observed effect: 100%, 75%, or 50%. These are hypothetical planning scenarios based on the observed contrast, not the study’s original design assumptions. The trial’s original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would give an 80% chance of detecting the specified effect under the assumptions, if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design concepts: power is the probability that a specified analysis would reject its null hypothesis under an assumed true effect, given the model and planning assumptions. It is not a measure of the probability that the result is correct.

The posted scenarios show that smaller target effects require more participants per arm to reach the same planned power. Detecting a fraction of the observed effect is a different and generally more demanding planning aim than detecting the full observed effect. Because the observed effect may be an uncertain estimate, planning from it can be optimistic, especially if the observed contrast is larger than the effect that would be expected in a future study. The figures are therefore useful as illustrations of how assumptions affect sample-size needs, rather than as a definitive design recommendation.

This is not observed power. Observed power calculated from the effect estimate already seen in the trial would add little information beyond the estimate and its uncertainty. The planning figures instead show how participant requirements change across the stated effect scenarios under the specified calculation assumptions. They do not indicate how the completed trial was originally planned, and they do not resolve whether the trial’s enrolled or analyzed sample was adequate for other endpoints or objectives.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 4.123; pooled standard deviation σ = 3.479.
2. n = 2 × (1.96 + 0.842)² × 3.479² / 4.123² = 11.2, rounded up to 12 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
delta <- 4.1226                      # observed difference in means
sigma <- 3.47878052412049                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(129623)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 12 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 27 (90% power)
 50% of observed effect: n per arm = 45 (80% power), 60 (90% power)
power.t.test: 12.2 
Simulated power at n = 12 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor-reported primary analysis is an ANOVA comparison of the mean difference between ibandronate and placebo. It reports a 95% confidence interval and a p-value below < 0.001. The simple unadjusted recalculation from the posted summary statistics gives a mean difference of 4.123 percentage points, with a 95% confidence interval from 2.962 to 5.284 and p < 0.001. The recalculated estimate and limits closely match the sponsor’s reported analysis.

The recalculation is a consistency check, not a replacement for the sponsor’s analysis. It is based on group-level summaries and does not reproduce any analysis choices that are not described in the registry record. The sponsor’s result is the trial’s reported analysis; the recalculation indicates that the headline contrast is numerically consistent with the posted group summaries. The registry does not provide enough detail to reconstruct every aspect of the ANOVA or assess its assumptions.

No discrepancy is flagged between the sponsor’s result and the recalculated comparison. That agreement supports reading the two as pointing to the same primary contrast, while keeping their methods distinct. The recalculation should not be treated as independent confirmation based on new data, since it uses the same posted trial summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and several secondary endpoints. This distinction matters because a primary outcome ordinarily carries the central confirmatory question, while additional outcomes can provide context or generate further questions. When multiple hypotheses are tested, the chance of finding at least one nominally notable result can rise. Statistical plans can address this through methods such as adjustment, an ordered testing strategy, or a clearly exploratory interpretation, but the registry record does not report whether any such approach was used.

The record does not report the original statistical analysis plan, a multiplicity procedure, interim analyses, or a sample-size justification. It also does not state whether there were protocol amendments affecting endpoints or analyses. Without those details, it is not possible to determine whether the posted primary and secondary analyses follow a prespecified strategy, or how the sponsor intended to interpret multiple outcomes together. This absence does not show that no plan existed; it means those details are not reported in the registry record.

The primary analysis population is described as randomized participants who received at least one dose and had baseline and at least one follow-up evaluation. That definition clarifies that the endpoint analysis required post-baseline information, but it is not a complete missing-data method. The record does not report the number of missing Month 12 measurements, reasons for missingness, imputation procedures, or sensitivity analyses. It also does not describe how participants with unsuitable scans were handled in the analysis. If missingness is related to outcome or treatment, the analyzed group may differ from the randomized group in ways that affect the estimated contrast.

The record does not state whether the primary analysis was intention-to-treat in the usual broad sense; it gives its own definition of the ITT population, including receipt of at least one dose and follow-up evaluation. That definition should be used when describing the analysis population rather than assuming it included every randomized participant. The endpoint group counts are smaller than the registered enrollment, but the registry does not provide the flow details needed to explain the difference, and no subtraction or reason for exclusion can be inferred from those counts alone.

Other unreported statistical details include covariate adjustment, model diagnostics, handling of protocol deviations, and procedures for dealing with any non-normality or unequal variability. These omissions limit independent evaluation of robustness. The sponsor-reported ANOVA result is available, and the summary-statistic recalculation is close to it, but agreement in the headline estimate does not answer questions about multiplicity, missingness, or the full analysis plan.

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: pyelonephritis (1.3%), chest pain (1.3%), upper limb fracture (1.3%), cellulitis (1.2%).

The registry’s adverse-event summary gives serious adverse events for 83 participants at risk in the placebo group, with 1 affected, and 77 participants at risk in the ibandronate group, with 3 affected. For other adverse events, the reported at-risk counts are 82 in the placebo group and 76 in the ibandronate group, with 41 and 40 affected, respectively. These are participant counts, not a complete account of event episodes or duration of exposure.

The registry lists pyelonephritis at 1.3%, chest pain at 1.3%, upper limb fracture at 1.3%, and cellulitis at 1.2% among the leading serious adverse-event terms. The record does not specify group attribution for these terms in the information, so they should not be assigned to one treatment arm. Death counts are not reported in the registry record.

These counts need cautious interpretation. The at-risk denominators differ across the safety summaries and are not the same as the primary endpoint analysis counts. The record does not provide event timing, exposure-adjusted rates, detailed definitions, attribution, or a complete narrative of serious events. Counts alone do not establish whether an event was caused by treatment or whether the groups differ meaningfully in safety.

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

The primary statistical result describes a difference in average relative change in lumbar spine bone mineral density at Month 12 between the analyzed ibandronate and placebo groups. The estimate is positive, its 95% confidence interval is above zero, and the sponsor reports a small p-value. These features indicate statistical evidence of a between-group difference under the reported analysis. They do not mean that each participant had the same outcome or that the average contrast necessarily predicts an individual participant’s result.

The result does not by itself establish clinical importance. The registry record does not report a threshold for a clinically meaningful change in this measurement, and statistical significance is not equivalent to clinical benefit. Nor does a group-average difference show how many participants improved, remained unchanged, or worsened; responder outcomes are listed, but numerical results for them are not reported in the registry record. The analysis also concerns a specific measurement site and time point, not every aspect of bone health or longer-term outcomes.

The findings should not be extended automatically to populations or settings beyond the stated study population. The record describes postmenopausal women with osteopenia and a monthly oral regimen, but does not provide detailed eligibility criteria, demographic characteristics, or subgroup results. It also does not report enough information about adherence, missing measurements, scan suitability, or analysis sensitivity to establish how robust the estimate is to those issues.

The primary endpoint is a measured outcome, not a direct summary of all benefits and harms. Safety interpretation requires attention to event definitions, exposure, timing, seriousness, and attribution. The adverse-event counts in the registry are limited summaries, and the record does not provide a complete account of deaths or all event details. The primary efficacy comparison therefore cannot be used alone to reach a benefit-harm conclusion.

In short, the posted data support a positive statistical contrast on the specified Month 12 lumbar spine measure in the analyzed participants. They do not settle the clinical meaning of that contrast, the completeness of outcome reporting, the impact of missing data, the results for all secondary outcomes, or the comparative safety profile. Those distinctions keep statistical description within what the registry record documents.

18. Why This Trial Matters Statistically

This study illustrates why the estimated effect, its uncertainty, and the analysis population need to be read together. A reported mean difference gives the scale and direction of the primary contrast, while the confidence interval indicates how precisely that contrast is estimated under the analysis. The p-value contributes evidence about compatibility with a null difference, but it cannot replace the estimate or interval as a description of the result.

The record also shows the value and limits of a simple recalculation from group summaries. The recalculated contrast is close to the sponsor-reported ANOVA result, which provides a useful numerical consistency check. Yet this agreement is not a full audit of the analysis: the registry does not report all model details, diagnostics, missing-data procedures, or the original analysis plan. Replication of a summary contrast and evaluation of an analysis strategy are different tasks.

Planning illustrations make another statistical point: the sample size required depends on the effect a study aims to detect and on its assumptions. The displayed scenarios use fractions of the observed effect, and smaller target effects require more participants per arm under those assumptions. Those calculations are distinct from the original design justification, which is not reported. They also are not retrospective measures of the completed trial’s power.

Finally, outcome multiplicity and incomplete reporting shape how secondary evidence should be weighed. Multiple listed outcomes can broaden the scientific question, but they also require a clear plan for interpretation and adjustment. The registry does not report such a strategy or numerical findings for most named secondary outcomes. Recognizing what is documented and what remains unreported is part of sound statistical interpretation, not merely a matter of presentation.

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.

A central limitation is the limited detail about the analysis process. The registry reports an ANOVA result but does not provide the model specification, covariates, diagnostics, or sensitivity analyses. The close agreement with the unadjusted recalculation supports consistency of the headline estimate with the posted summaries, but cannot verify the analysis assumptions or choices.

The endpoint analysis population required participants to have at least one follow-up evaluation. The record does not report the number or reasons for missing Month 12 measurements, the handling of unsuitable scans, or any imputation or sensitivity analysis. As the endpoint relies on DEXA measurements, the stated scan suitability criteria are relevant, but the number of scans affected and their distribution by group are not reported. The difference between enrollment and endpoint analysis counts cannot be explained from the registry information alone.

Important design and planning details are also absent. The original sample-size justification, allocation procedures, masking procedures, interim analysis plans, and the full statistical analysis plan are not reported in the registry record. The record does not describe adherence, treatment exposure in detail, or protocol deviations. These omissions constrain assessment of the trial’s conduct and robustness without establishing that any particular problem occurred.

Most secondary outcomes have no numerical results in the record, despite being listed. The multiplicity strategy is not reported, so the inferential status of secondary findings cannot be determined. The safety summaries include participant counts and selected event terms, but not full event timing, attribution, exposure-adjusted comparisons, or death counts. Together, these limitations mean the primary result can be described, but broader claims about all outcomes, long-term effects, or comparative safety are not supported by the documented details.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Bonviva (Ibandronate) Once Monthly in Post-Menopausal Women With Osteopenia — NCT00129623.
• Registry record last updated 2016-01-11; status last verified 2015-12.
• Results first posted 2016-01-11.
• 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

NCT00129623 is a completed Phase 4, randomized, double-blind, parallel-group, multicenter study sponsored by Hoffmann-La Roche. It compared oral ibandronate 150 mg once monthly with monthly placebo in postmenopausal women with osteopenia. Registered enrollment was 160; the study started in 2005-12 and had primary completion in 2007-12.

The primary endpoint was relative change from baseline in mean lumbar spine bone mineral density at Month 12. The sponsor-reported ANOVA gives a positive between-group mean difference, with a 95% confidence interval above zero and p < 0.001. An unadjusted summary-statistic recalculation is close to that result. The registry describes the primary analysis population but does not report a full account of missing data, the original sample-size rationale, or the complete analysis plan. Secondary outcomes are listed, but numerical results for most are not reported in the registry record.