DIVA Study - A Study of Different Regimens of Intravenous Administration of Bonviva (Ibandronate) in Women With Post-Menopausal Osteoporosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for DIVA Study - A Study of Different Regimens of Intravenous Administration of Bonviva (Ibandronate) in Women With Post-Menopausal Osteoporosis (NCT00048074), a randomized phase 3 study. The primary outcome is Relative Percent Change From Baseline in Mean Bone Mineral Density (BMD) of Lumbar Spine (L2-L4) at 12 Months.

2. Clinical Question

The trial addressed whether intravenous ibandronate regimens produced different changes in lumbar-spine bone mineral density from daily oral ibandronate in women with post-menopausal osteoporosis. Its primary endpoint was the relative percent change from baseline in mean lumbar-spine BMD at Month 12. The registry describes the primary analysis population as per protocol: randomized participants who received at least one dose, had at least one efficacy follow-up measurement, and had no major protocol violations.

The registry summary says participants also received daily calcium and vitamin D supplementation. The listed treatment groups therefore compare ibandronate regimens against one another in the context of that supplementation, rather than comparing ibandronate with no treatment. The primary measurement was a bone-density outcome; the clinical question is consequently about this measured endpoint, not directly about fractures or other outcomes that are not listed as the primary endpoint.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group study sponsored by Hoffmann-La Roche. The registry records an enrollment of 1395 and a completed status. The recorded start was 2002-06 and primary completion was 2005-05. The official title describes a comparison of different intravenous Bonviva regimens on lumbar BMD in women with osteoporosis; the study summary also describes comparison with daily oral administration.

Three regimens are described. One group received daily oral ibandronate 2.5 mg and intravenous placebo. A second received intravenous ibandronate 2 mg every 2 months and daily oral placebo. A third received intravenous ibandronate 3 mg every 3 months and daily oral placebo. The registry describes daily calcium and vitamin D supplementation. Because the groups differ in both administration route and dosing schedule, the contrast is between treatment regimens as a whole; the record does not describe a design that isolates route or frequency as separate effects.

Random allocation and double masking are recorded, but details of the allocation sequence, concealment procedures, and how masking was maintained are not reported in the registry record. The record identifies a parallel model, meaning participants were assigned to a group for comparison rather than described as crossing between regimens. It does not report the original sample-size justification, planned enrollment target in the formal design, or the statistical plan in sufficient detail to establish the intended analysis beyond the posted endpoint and analysis entries.

The registry summary anticipated treatment for 2+ years. The primary endpoint was assessed at Month 12, and a lumbar-spine BMD outcome was also listed at Month 24. The registry lists 16 outcome measures and reports 15 secondary results as posted. The posted primary analysis is explicitly described as per protocol, which limits its interpretation to the participants meeting the stated efficacy and protocol criteria.

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: Out of the 1395 participants who were randomized into the study, only 1382 participants received at least one dose of trial treatment and had at least one follow-up assessment as 4 participants did not have safety follow-up and 9 participants did not receive trial treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per protocol population: Participants who were randomized, received at least one dose of study medication and had at least one efficacy (BMD or serum CTX) follow-up data point and did not have any major violations of the protocol.

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: Safety Population: All participants who were randomized and had at least one dose of study drug, whether withdrawn prematurely or not, and who had at least one follow-up data point were included.

6. Primary Endpoint

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

The primary endpoint was relative percent change from baseline in mean lumbar-spine BMD, measured at the L2-L4 region, at Month 12. The registry says BMD was measured by a single dual-energy x-ray absorptiometry scan at screening and at Month 12. The change was defined as the relative difference between the last individual measurement available at 12 months and baseline, expressed as a percent of baseline BMD.

BMD is a continuous measurement: each participant's result can take a range of values, rather than being only an event/no-event outcome. The registry reports the group mean and standard deviation for this endpoint. In general, a continuous measure can capture changes across the measurement scale and can be useful when a treatment is expected to alter a biological or anatomical measurement. That general rationale does not make BMD equivalent to a direct measure of fracture occurrence or patient experience.

The endpoint was used to compare average change under the randomized regimens. Its relative-change definition accounts for each measurement in relation to the participant's baseline value, while the reported group summaries describe average percent change within the analysis population. Interpretation depends on the measurement procedures, the population included, and the uncertainty around the between-group contrast. The registry does not report a minimally important difference for this endpoint, so the numerical contrasts alone do not establish how large a change would be clinically meaningful.

7. Results Posted in the Registry

• Ibandronate 2mg q 2 mo IV: mean 5.09 versus 3.82 on control; difference 1.27 (95% CI 0.70 to 1.83), standardized effect d = 0.33; z-test p = <0.001.
• Ibandronate 3mg q 3 mo IV: mean 4.82 versus 3.82 on control; difference 1.00 (95% CI 0.45 to 1.55), standardized effect d = 0.26; 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.

Relative Percent Change From Baseline in Mean BMD of Lumbar Spine (L2-L4) at 24 Months

• 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 2mg q 2 mo IV: mean 6.40 versus 4.84 on control; difference 1.56 (95% CI 0.82 to 2.29), standardized effect d = 0.32; z-test p = <0.001.
  • Ibandronate 3mg q 3 mo IV: mean 6.28 versus 4.84 on control; difference 1.44 (95% CI 0.69 to 2.19), standardized effect d = 0.29; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ibandronate 2mg q 2 mo IV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ibandronate 3mg q 3 mo IV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering lumbar-spine BMD at 24 months, proximal-femur BMD, serum CTX, and the proportions of participants whose lumbar-spine or total-hip BMD was at least baseline. These outcomes extend the primary question across a later time point, other skeletal measurements, a biochemical measure, and threshold-based summaries. They are related to the primary BMD result, but they address different measurements and time points and should not be treated as interchangeable replications of the primary endpoint.

The posted Month 24 lumbar-spine summaries follow the same broad direction as the primary outcome: the reported mean relative changes are positive in all three groups, and the intravenous-group means are higher than the daily oral group's mean. This directional consistency can be considered alongside the primary result, while recognizing that it is a separate endpoint and time point. Numerical results for the other listed secondary outcomes are not reported in the registry record available for this analysis, so no overall claim about their effects or consistency can be made from their names alone.

General explanation: when a study tests many outcomes or makes many comparisons, the chance of at least one apparently notable result can increase. Unadjusted secondary results therefore usually carry less confirmatory weight than a prespecified primary result, particularly when the analysis plan and multiplicity procedure are not reported. Secondary outcomes can still help describe the breadth of the evidence and identify questions for further study, but their interpretation should account for the number of tests, their relationship to the primary endpoint, and whether the findings were prespecified.

The registry lists 16 outcome measures and reports 15 secondary results as posted, but it does not report a multiplicity adjustment in the information available for these results. The secondary endpoints should therefore be read as complementary evidence, not as a set of independent tests that automatically strengthens the primary conclusion.

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

• Relative Percent Change From Baseline in Mean BMD of Lumbar Spine (L2-L4) at 24 Months
• Absolute Change From Baseline in Mean BMD of Lumbar Spine (L2 - L4) at Month 12 and Month 24
• Relative Percent Change From Baseline in BMD of Proximal Femur (Consisting of Total Hip, Trochanter, and Femoral Neck) at Month 12 and 24
• Absolute Change From Baseline in BMD of Proximal Femur (Consisting of Total Hip, Trochanter, and Femoral Neck) at Month 12 and 24
• Relative Change From Baseline in Serum C-telopeptide of Alpha-chain of Type I Collagen (CTX) at Month 6, 12, and 24
• Absolute Change From Baseline in Serum CTX at Month 6, 12, and 24
• Percentage of Participants With Mean Lumbar Spine (L2 - L4) BMD Above or Equal to Baseline at Month 12 and 24
• Percentage of Participants With Total Hip BMD Above or Equal to Baseline at Month 12 and 24

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

The primary endpoint is continuous, so the group summaries use means and standard deviations. A mean is the average endpoint value within a group. A standard deviation describes how dispersed individual measurements are around that average; it is not the uncertainty in the mean and is not a confidence interval. In the posted primary summaries, each group's mean is a relative percent change in BMD, and the between-group estimate is expressed in the same endpoint units.

The recalculated mean difference compares the intravenous group's mean with the daily oral group's mean. A positive estimate in these comparisons means the reported average change was higher in the intravenous group. This is a contrast of group averages, not a statement that every participant in one group had a higher result than every participant in the other group. The 95% confidence interval describes statistical uncertainty around the estimated difference under the calculation's assumptions.

What does the recalculation include?

The recalculated comparisons are simple, unadjusted estimates based on the posted group summaries. They do not represent a new randomized trial or an adjusted analysis. They summarize the difference between the reported means and use the posted sample sizes and standard deviations to estimate uncertainty. The registry's sponsor-reported analysis uses ANOVA and is reported separately. Because that is the trial's own analysis, it takes precedence over the simple recalculation when describing the sponsor's inferential results. The record does not give enough detail to reconstruct every feature of the ANOVA model.

How should p-values be read?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, assuming the model and other analysis conditions hold. A value reported as p < 0.001 does not mean that the null hypothesis has less than a 0.001 probability of being true, nor does it measure the probability that the findings occurred by chance. The registry gives unadjusted p-values for the recalculated comparisons and p-values for the sponsor-reported comparisons. The record does not report a multiplicity adjustment for these tests, so the p-values should not be interpreted as if they necessarily account for all outcomes and comparisons.

Why do the analysis population and missing observations matter?

Randomization aims to make treatment groups comparable at allocation. An analysis restricted to participants who meet post-randomization criteria can depart from that original randomized comparison if inclusion is related to treatment or outcome. The primary endpoint population is defined as per protocol: participants were randomized, received at least one dose, had at least one efficacy follow-up measurement, and had no major protocol violations. The registry reports the group sample sizes used for the posted primary endpoint, but the reasons participants did not contribute to this analysis and the handling of missing measurements are not reported in the registry record.

In general, missing-data methods matter because results can differ depending on whether missing values are excluded, imputed, or handled through a model. The registry record does not report the missing-data method for the primary result. It also does not describe sensitivity analyses to assess whether conclusions change under alternative assumptions about missing outcomes. These omissions limit assessment of robustness, rather than proving that the analysis was necessarily biased.

Why do non-inferiority and equivalence require additional context?

In general, a non-inferiority analysis asks whether the treatment difference is not worse than a prespecified margin, while an equivalence analysis asks whether the difference lies within prespecified bounds in both directions. The margin or bounds are central: a p-value alone is not enough to identify the clinical threshold or independently verify a conclusion. The registry labels the sponsor's ANOVA comparisons as non-inferiority or equivalence, but the margin, decision rule, and detailed hypotheses are not reported in the registry record. The reported estimates and intervals can be described, but the label alone does not establish which criterion was applied or whether it was satisfied.

What does over-dispersion mean for a continuous endpoint?

General explanation: over-dispersion is most often discussed when a statistical model assumes less variability than the data actually show, particularly for counts. If variability is underestimated, standard errors can be too small and confidence intervals too narrow. For this trial's primary endpoint, the registry reports a continuous measure and standard deviations; it does not report an over-dispersion adjustment or indicate that over-dispersion was a concern. The relevant general lesson is that uncertainty estimates depend on how well the model represents the observed variability. A standard deviation and a model-based standard error serve different roles.

The registry does not report whether interim analyses were planned or conducted, whether the primary analysis was prespecified in a publicly available protocol, or the original statistical analysis plan. Those details cannot be inferred from the posted endpoint and results. The available interpretation should therefore stay close to the reported group summaries, the sponsor's analysis, and the limitations recorded for the analysis population and missing-data methods.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated between-group difference. The sponsor-reported 95% confidence interval for the 2 mg every 2 months intravenous comparison extends from 0.701 to 1.814. For the 3 mg every 3 months comparison, it extends from 0.471 to 1.578. The simple unadjusted recalculations give intervals from 0.702 to 1.833 and from 0.445 to 1.553, respectively. The recalculated intervals are not substitutes for the sponsor's own analysis; they are unadjusted summaries derived from the posted group statistics.

In general, a 95% confidence interval is produced by a method that, over repeated use under its assumptions, would cover the underlying parameter in 95% of such intervals. It is not a 95% probability statement about the fixed true difference after this particular interval has been calculated. The interval expresses uncertainty about the average contrast, not the spread of individual participant outcomes; the standard deviations describe that within-group spread.

The reported intervals are entirely on the positive side for both sponsor comparisons, while the registry also reports p < 0.001 for each. This supports evidence of a positive mean difference under the sponsor's stated analysis, but it does not answer whether that difference satisfies a clinical or non-inferiority threshold. The non-inferiority margin and a threshold for clinical importance are not reported in the registry record. Thus, the interval can inform the likely range of the statistical contrast without resolving the practical importance of that contrast.

The interval widths also reflect the observed variability and the analyzed group sizes, as well as the method used. Precision is not the same as absence of bias: a narrow interval cannot correct limitations from the analysis population, missing-data handling, or outcome measurement. Nor does an interval for mean BMD change describe the uncertainty in fracture outcomes, which are not the primary endpoint.

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 illustrations based on the observed effect, not the trial's original design calculation. For this continuous endpoint, the reported figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set at the stated fraction of the observed effect. The original trial's sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect is the true one and the model assumptions hold. The 90% power column uses a higher probability of detecting that effect and consequently gives a larger planning requirement. These are design calculations, not estimates of the chance that the completed trial found a true effect.

Rows planning for 100% of the observed effect use the full observed contrast as the assumed target. Rows planning for 75% or 50% of the observed effect use smaller target differences. Smaller effects need more participants because they are harder to distinguish from random variation when variability and other assumptions are held constant. The displayed quantities are planning illustrations based on the observed results; they are not observed power and should not be read as the trial's actual planned enrollment or as evidence that the original design was adequately powered.

Use the figures as conditional planning scenarios rather than as a recommendation for a future study. A new design would need its own clinically justified target effect, variability assumptions, allocation plan, analysis method, and allowance for missing outcome data. The registry does not report the original assumptions needed to compare these illustrations with the trial's own design process.

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 = 1.267; pooled standard deviation σ = 3.866.
2. n = 2 × (1.96 + 0.842)² × 3.866² / 1.267² = 146.1, rounded up to 147 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 <- 1.2673                      # observed difference in means
sigma <- 3.86589565149039                     # 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(48074)
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 = 147 (80% power), 196 (90% power)
 75% of observed effect: n per arm = 260 (80% power), 348 (90% power)
 50% of observed effect: n per arm = 585 (80% power), 783 (90% power)
power.t.test: 147 
Simulated power at n = 147 per arm: 0.801 (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 registry reports the sponsor's comparisons using ANOVA and labels them as non-inferiority or equivalence analyses. For the 2 mg every 2 months intravenous group versus daily oral treatment, the reported mean difference is 1.257, with a 95% confidence interval from 0.701 to 1.814 and p < 0.001. For the 3 mg every 3 months intravenous group, the reported mean difference is 1.025, with a 95% confidence interval from 0.471 to 1.578 and p < 0.001.

The simple unadjusted recalculations from the posted summary statistics are close to, but not identical with, the sponsor's reported estimates. Such differences can arise because a recalculation from group summaries need not reproduce the sponsor's full analysis method. The registry does not provide enough model detail to account for every difference. The discrepancy flag is false, and the sponsor's own analysis takes precedence for interpreting the reported trial analysis.

The non-inferiority or equivalence label requires context beyond the estimates and p-values. The registry does not report the margin, bounds, or decision rule, so the sponsor's classification can be reported but not independently evaluated against a stated threshold. A statistically positive mean difference is not, by itself, proof that a non-inferiority or equivalence criterion was met.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or treatment comparisons are assessed. In general, repeated testing can increase the chance of at least one small p-value even when the corresponding null hypotheses are true. A prespecified testing hierarchy or adjustment can address that issue, but the registry record does not report a multiplicity procedure for the posted comparisons. The primary endpoint is clearly identified, but the detailed statistical analysis plan, the hierarchy among secondary outcomes, and any family-wise error or false-discovery strategy are not reported in the registry record.

The registry reports two sponsor comparisons against the daily oral group for the primary endpoint, as well as a broad set of secondary outcomes. The reported p-values are not described as multiplicity-adjusted. The secondary findings consequently warrant a more exploratory interpretation than the primary result, especially where several endpoints and time points are involved. This does not show that a multiplicity adjustment was absent from the full trial analysis; it means the adjustment is not reported in the registry record.

The primary analysis population is per protocol and excludes participants who did not meet the specified follow-up and protocol criteria. The registry does not report the missing-data method, the reasons for missing primary endpoint data, or sensitivity analyses under alternative missing-data assumptions. It therefore is not possible to assess from the record whether the primary estimate is robust to missing outcomes or whether exclusion criteria affected the randomized comparison.

The registry reports enrollment and the analyzed sample sizes, but the original sample-size justification and design assumptions are not reported in the registry record. Interim analyses, any stopping rules, and the detailed prespecification of the sponsor's ANOVA are also not reported. These gaps limit independent assessment of the analysis process. They should be kept distinct from the observed endpoint summaries: lack of reporting is not evidence that a procedure was or was not performed.

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: myocardial infarction (0.9%), ankle fracture (0.7%), asthma (0.7%), osteoarthritis (0.7%), ovarian cyst (0.6%).

The registry lists serious adverse event participants at risk and affected for each treatment group. For daily oral ibandronate, 465 participants were at risk and 67 were affected; for intravenous ibandronate 2 mg every 2 months, 448 were at risk and 73 were affected; for intravenous ibandronate 3 mg every 3 months, 469 were at risk and 62 were affected. These are group counts, not calculated rates. The registry also lists other adverse event counts of 301, 316, and 284, respectively, with the corresponding at-risk groups reported as 465, 448, and 469.

The serious-event terms with the largest listed percentages are myocardial infarction, 0.9%; ankle fracture, 0.7%; asthma, 0.7%; osteoarthritis, 0.7%; ovarian cyst, 0.6%; and breast cancer, 0.4%. These percentages are registry entries and should not be interpreted as proof that the study treatment caused the events. The record does not report deaths in the posted safety information.

Safety counts depend on the registry's event definitions, observation period, and reporting procedures. The registry record does not provide enough detail to compare event timing, severity beyond the serious-event classification, or causal attribution. The counts should be read as descriptive safety information, not as a stand-alone measure of comparative risk.

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

The posted primary results show positive average relative lumbar-spine BMD changes in all three groups at Month 12. The two intravenous groups have higher reported means than daily oral ibandronate, and the sponsor's ANOVA estimates are positive with confidence intervals that remain above zero. The registry also reports p < 0.001 for both sponsor comparisons. These findings describe the measured endpoint in the registry's per-protocol analysis population.

That statistical pattern does not by itself establish the clinical importance of the differences. The registry does not report a minimally important BMD difference or the non-inferiority margin and decision rule. The outcomes listed center on BMD and serum CTX; the primary result is not a direct measure of fractures, symptoms, function, or quality of life. A change in a measurement should not be translated into an effect on those outcomes without corresponding evidence.

The record describes randomized, double-blind allocation, which supports comparison of assigned regimens, but the primary analysis is per protocol rather than an explicitly reported intention-to-treat result. Missing-data methods and sensitivity analyses are not reported in the registry record. These limitations affect how confidently the results can be generalized to all randomized participants and how robust the estimate is to incomplete follow-up.

The appropriate interpretation is therefore bounded: the posted data indicate differences in average BMD change between the treatment groups under the reported analysis. They do not alone establish a broader treatment benefit, an effect on fracture risk, or the success of a non-inferiority claim under a prespecified margin that is not reported. Safety counts are descriptive and do not establish causation. No medical decision should be based on this statistical summary alone.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares multiple administration regimens using a continuous endpoint and reports both group-level summaries and sponsor-reported inferential analyses. The primary endpoint's definition, measurement time, and analysis population are specified in the registry, allowing the numerical comparison to be interpreted in relation to the intended BMD measure rather than as an unspecified outcome.

The record also illustrates why a reported trial analysis and a recalculation from summary statistics are not interchangeable. The simple unadjusted contrasts are close to the ANOVA estimates but differ slightly. The sponsor's analysis is the relevant trial-reported inference, while recalculation provides a transparent way to examine the posted means and variability. Neither approach removes the need to understand the analysis population, model, or prespecified decision criteria.

Its non-inferiority or equivalence classification highlights the importance of reporting the margin and analysis rules. An estimate, confidence interval, and small p-value do not have a complete interpretation without the threshold that defines an acceptable difference. The registry's limited reporting of that context, multiplicity, missing-data handling, and original sample-size assumptions marks a boundary on what can be independently assessed.

Finally, the distinction between a bone-density endpoint and clinical outcomes is central. Statistical evidence about a measurement can be precise while remaining incomplete for questions about fractures or patient experience. Reading the result carefully means attending both to the strength of the numerical comparison and to what the endpoint and registry record do not establish.

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.

The primary result is based on a per-protocol population. That population is defined by receipt of at least one dose, efficacy follow-up, and absence of major protocol violations, so it is not identical by definition to all randomized participants. The registry does not report a complementary intention-to-treat estimate or the reasons for exclusions and missing endpoint measurements. The effect of these features on the comparison cannot be determined from the record.

The sponsor's analysis is identified as ANOVA and as non-inferiority or equivalence, but the registry does not report the margin, bounds, model details, or full decision rule. The original statistical analysis plan, any interim analyses, and the original sample-size rationale are also not reported in the registry record. This limits independent evaluation of prespecification and of the criteria used to interpret the comparisons.

The interventions compare regimens that differ in route and dosing frequency. The registry therefore supports comparisons of those bundled regimens, not separate conclusions about the effect of route alone or schedule alone. The primary endpoint is lumbar-spine BMD at Month 12; the registry's named secondary measures include other BMD sites and serum CTX, but the listed primary outcome is not a fracture endpoint. A fracture outcome is not reported among the named endpoints in the registry record.

The posted safety data are descriptive counts and listed event percentages. The record does not provide sufficient information about event timing, causal assessment, or the details of exposure and follow-up to support a comprehensive comparative safety analysis. These are reporting and design-interpretation limits; they do not negate the reported results, but they narrow the conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: DIVA Study - A Study of Different Regimens of Intravenous Administration of Bonviva (Ibandronate) in Women With Post-Menopausal Osteoporosis — NCT00048074.
• Registry record last updated 2016-02-03; status last verified 2016-01.
• Results first posted 2016-02-03.
• 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

NCT00048074, the DIVA Study, was a completed Phase 3 randomized, double-blind, parallel-group trial sponsored by Hoffmann-La Roche. It compared daily oral ibandronate 2.5 mg with intravenous ibandronate 2 mg every 2 months and intravenous ibandronate 3 mg every 3 months in women with post-menopausal osteoporosis. The registry records enrollment of 1395.

The primary endpoint was relative percent change from baseline in mean lumbar-spine BMD at Month 12, analyzed in a per-protocol population. The sponsor reported positive ANOVA mean differences for both intravenous regimens versus daily oral treatment, with p < 0.001 for each. The registry labels these comparisons as non-inferiority or equivalence, but the margin and decision rule are not reported in the registry record.

The results concern BMD change and should be interpreted alongside the per-protocol analysis, unreported missing-data methods, and limited detail about multiplicity and the original analysis plan. They do not alone establish effects on fractures or other unlisted clinical outcomes.