Vitamin D Levels in Children With IBD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vitamin D Levels in Children With IBD (NCT00621257), a randomized na study. The primary outcome is Treatment of Low 25 Hydroxy Vitamin D Levels in Pediatric Patients With Inflammatory Bowel Disease.

2. Clinical Question

The study addresses a measurement and treatment question in a pediatric population with inflammatory bowel disease. Its focus is serum 25OHD, a measure of vitamin D stores, rather than a direct clinical measure of bone health or IBD activity. The registry summary gives the rationale that vitamin D levels may be lower among children with IBD and that vitamin D is relevant to bone health and inflammation. Those statements describe the study rationale, not results established by this trial.

The intervention descriptions include both treatment and maintenance strategies, but the available record does not describe the relationship between these groups in enough detail to establish whether they were sequential stages, separate cohorts, or otherwise connected. The primary comparison concerns the six-week treatment regimens. The maintenance outcome is recorded separately at 12 months. These distinctions matter when interpreting the study question: results for short-term change in a blood measure do not, by themselves, answer whether bone health or disease outcomes changed.

3. Trial Design

The registry record describes a randomized, parallel-design trial with no masking. It lists an overall enrollment of 134 and status as terminated. The start is recorded as 2008-01, and primary completion as 2011-03. The phase is listed as NA. The record identifies Boston Children's Hospital as sponsor.

Three treatment arms are listed for the primary outcome. Treatment A used 2,000 IU/day of ergocalciferol orally for 6 weeks and was designated the control. Treatment B used 2,000 IU/day of cholecalciferol orally for 6 weeks. Treatment C used 50,000 IU of ergocalciferol orally once a week for 6 weeks. The posted arm sizes were 24, 24, and 23, respectively. The primary outcome timeframe was 6 weeks.

Two maintenance arms are also listed. Maintenance A used 400 IU/day of ergocalciferol orally over 2 years and was the control. Maintenance B used 2,000 IU/day from November 1 to April 30 and 1,000 IU/day for the remainder of the year, also over 2 years. The secondary outcome was recorded at 12 months, with 32 participants listed for Maintenance A and 31 for Maintenance B. The registry record does not explain how the maintenance regimens relate to the treatment regimens, or why the study was terminated.

Random allocation can reduce systematic differences between groups at the outset when implemented appropriately, but randomization details, allocation concealment, and the method used to assign participants are not reported in the registry record. Because masking is listed as none, the study was open-label. Blinding of outcome assessment is not reported. The original sample-size justification, planned analysis methods, and reasons for termination are also not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Treatment of Low 25 Hydroxy Vitamin D Levels in Pediatric Patients With Inflammatory Bowel Disease, measured over 6 weeks.

The primary endpoint is the change in serum 25OHD levels after treatment with vitamin D formulations for 6 weeks in pediatric patients with inflammatory bowel disease. The measurement unit is ng/ml, and the outcome is summarized as a mean with standard deviation. The registry describes 25OHD as the most abundant vitamin D metabolite and states that its concentration in serum reflects vitamin D stores.

A continuous blood measurement can capture the amount of change across a range of values, rather than reducing the result to a yes-or-no category. Comparing mean changes across treatment arms can therefore describe how the groups differed in the measured serum outcome over the stated timeframe. The posted means are 9.3 for Treatment A, 16.4 for Treatment B, and 25.4 for Treatment C; the corresponding standard deviations are 1.8, 2.0, and 2.5.

The registry outcome description identifies change as the endpoint, but does not state the exact calculation used to obtain each participant's change, such as which baseline and follow-up measurements were included or how missing measurements were handled. Nor does it define a target 25OHD level. The endpoint is a measure of vitamin D stores, not a direct measure of bone health, IBD activity, symptoms, or quality of life. Although the study rationale mentions those broader topics, the posted primary endpoint alone cannot establish effects on them.

7. Results Posted in the Registry

• Treatment B: mean 16.40 versus 9.30 on control; difference 7.10 (95% CI 6.02 to 8.18), standardized effect d = 3.73; z-test p = <0.001.
• Treatment C: mean 25.40 versus 9.30 on control; difference 16.10 (95% CI 14.85 to 17.35), standardized effect d = 7.42; 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.

Maintenance of 25 Hydroxy Vitamin D Levels in Pediatric Patients With Inflammatory Bowel Disease

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Maintenance B: 9.7% (3/31) versus 9.4% (3/32) on control; risk difference 0.3 percentage points (95% CI -14.2 to 14.8), risk ratio 1.03 (0.23–4.73); unadjusted two-proportion z-test p = 0.967.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Maintenance B and the control. The interval gives the range of effects that remain compatible with the data.

The registry record contains one posted secondary outcome, maintenance of 25 Hydroxy Vitamin D Levels in pediatric patients with inflammatory bowel disease, assessed at 12 months. It is recorded as a participant count in the two maintenance arms. The arm counts and unadjusted comparison do not indicate a clear separation between the regimens in the posted outcome. The record does not define the threshold or rule used to determine that a participant maintained the level, which limits interpretation of what the count represents.

This secondary outcome is related to the primary outcome because both concern vitamin D status. However, it addresses a different timeframe and a different treatment stage, and it is not the same measure as mean change in serum 25OHD after 6 weeks. Consequently, the primary result cannot be treated as direct evidence for the maintenance outcome, and the maintenance comparison does not negate or confirm the short-term treatment contrast. The record also does not clarify whether participants in the maintenance arms had previously received one of the short-term treatment regimens.

The secondary comparison is unadjusted. Unadjusted secondary results generally carry less weight than a prespecified primary result because multiple outcomes and comparisons create more opportunities for chance findings, and the registry record does not report a multiplicity strategy. The record lists no reported analyses and provides no analysis plan, making it difficult to determine whether this outcome and its comparison were prespecified in the same way as the primary outcome.

These limitations are especially relevant when an outcome's definition is incomplete. Without the maintenance criterion, analysis population, missing-data rules, and inferential method, a participant count cannot be fully evaluated. The broad pattern should therefore be read as a limited descriptive result rather than as a definitive assessment of long-term maintenance or as a direct clinical conclusion.

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

• Maintenance of 25 Hydroxy Vitamin D Levels in Pediatric Patients With Inflammatory Bowel Disease

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: serum 25OHD change is summarized with a mean and standard deviation. A mean describes the central value in a group, while a standard deviation describes how dispersed individual observations are around that mean. These measures give different information: the mean locates the group summary, and the standard deviation describes variability among observations. The posted standard deviations are 1.8 for Treatment A, 2.0 for Treatment B, and 2.5 for Treatment C.

What does a mean difference represent?

A mean difference subtracts one group's mean from another group's mean. The posted comparisons use Treatment A as the reference: the mean difference is 7.1 ng/ml for Treatment B and 16.1 ng/ml for Treatment C. These are comparisons of group summaries, not statements about the change experienced by every participant. The registry record does not describe adjustment for baseline values or other participant characteristics, so the posted estimates should be read as unadjusted group comparisons.

How should the p-values be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. The posted primary comparisons have unadjusted p-values of <0.001. The test procedure and its assumptions are not reported in the registry record, so the p-values cannot be independently evaluated from the description alone.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the observed estimate under the method's assumptions. For Treatment B versus Treatment A, the posted interval is 6.024 to 8.176 ng/ml; for Treatment C versus Treatment A, it is 14.85 to 17.35 ng/ml. The ranges communicate uncertainty around each estimate, while the point estimates alone do not. A confidence interval is not a guarantee that the true value lies within the particular calculated interval. Its coverage interpretation depends on the method and assumptions.

What is a standardized effect?

The comparisons also include standardized effect sizes, which express a difference relative to the variability of the measurements. The posted standardized values are 3.732 for Treatment B and 7.417 for Treatment C. Standardizing can make effects from different measurement scales easier to compare, but it does not replace the original-unit results. The registry record does not report these standardized values as part of a formal trial analysis, nor does it state an interpretation threshold for them.

Why do assumptions and analysis details matter?

In a randomized trial, random allocation is intended to make groups comparable on average. That protection depends on how the randomization was implemented and how participants were retained and analyzed. The registry record does not report allocation concealment, the analysis population, whether the analysis followed assignment as randomized, or how missing outcomes were handled. The listed allocation is randomized, but the additional details needed to assess those aspects are not reported in the registry record.

The registry record lists no reported analyses and does not identify a statistical model, test, covariate adjustment, or multiplicity procedure. The posted comparison estimates and intervals can still be described, but the absence of a named analysis method limits assessment of whether the chosen method matched the design and data. In general, a statistical method should account for the outcome type, the allocation structure, and relevant features of how measurements were collected. That is a general methodological principle, not a claim about what was done in this trial.

The secondary outcome is a participant count at 12 months, making it a binary-type outcome if each participant is classified as meeting or not meeting a criterion. The registry record does not give the criterion used to classify maintenance of 25 Hydroxy Vitamin D Levels. The posted comparison includes a risk difference and relative measures, but the record does not name the inferential method used to obtain them. For a binary outcome, the choice of measure affects how a comparison is expressed: a risk difference describes an absolute contrast, whereas a risk ratio or odds ratio describes a relative contrast. These are general statistical distinctions.

Finally, the planning illustrations use an assumed two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They are based on stated fractions of the observed effect. These assumptions describe the illustrations, not the trial's original design. The original design's sample-size assumptions and justification are not reported in the registry record.

11. Confidence Intervals and Precision

The primary comparisons have confidence intervals that quantify uncertainty around the estimated mean differences. For Treatment B compared with Treatment A, the estimate is 7.1 ng/ml, with a 95% confidence interval of 6.024 to 8.176 ng/ml. For Treatment C compared with Treatment A, the estimate is 16.1 ng/ml, with a 95% confidence interval of 14.85 to 17.35 ng/ml. The intervals are relatively concentrated around their respective estimates, but precision should be judged in light of the analysis assumptions and the completeness of the record.

In general, a confidence interval reflects both the estimated effect and the uncertainty arising from sampling variability under a specified method. It is not a range of values that contains every participant's outcome, and it does not capture every possible source of uncertainty. For example, it cannot by itself address bias from unreported missing-data decisions, deviations from the intended allocation, or selective reporting.

The interval endpoints for each primary comparison are above zero, the value corresponding to no mean difference. This is consistent with the posted unadjusted p-values of <0.001. The intervals do not show how much of the observed difference would matter clinically; the record does not specify a minimum important difference for serum 25OHD.

For the secondary maintenance comparison, the risk-difference interval ranges from -0.142 to 0.148. Its span includes zero, so the posted interval is compatible with no risk difference as well as differences in either direction under the method's assumptions. The registry record does not report a confidence-interval method for any outcome. These intervals should therefore be read as the posted summaries, not as a complete account of uncertainty or as evidence about unmeasured outcomes.

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 describe participants per arm for the two-arm comparisons, not total participants across both arms and not total events. The primary comparisons are continuous-outcome illustrations, and the maintenance comparison is a binary-outcome illustration. The registry record's planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants. These are planning concepts, not guarantees of a result. They depend on the assumed effect, variability, significance level, allocation, and statistical approximation.

The displayed rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects need more participants because they are harder to distinguish from random variation. The maintenance illustration produces very large sample-size figures because the observed risk difference is small; that is a consequence of the stated planning assumptions and observed effect, not a recommended enrollment target. Very small calculations for the primary outcome likewise reflect the size of the observed contrasts and should not be treated as a design recommendation.

This is not observed power. It is a planning illustration based on the observed effect, and the registry record does not establish that these calculations informed the original trial design. In general, planning based on an observed effect can be unstable, particularly when the estimate comes from a limited sample. The figures are best read as conditional illustrations of how assumed effect size relates to planning requirements.

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 = 7.100; pooled standard deviation σ = 1.903.
2. n = 2 × (1.96 + 0.842)² × 1.903² / 7.100² = 1.1, rounded up to 2 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 <- 7.1                      # observed difference in means
sigma <- 1.90262975904404                     # 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(621257)
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 = 2 (80% power), 2 (90% power)
 75% of observed effect: n per arm = 3 (80% power), 3 (90% power)
 50% of observed effect: n per arm = 5 (80% power), 7 (90% power)
power.t.test: 2.5 
Simulated power at n = 2 per arm: 0.517 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and a secondary outcome, but does not report a statistical analysis plan or a strategy for handling multiple comparisons. Multiple testing can increase the chance that at least one comparison appears statistically unusual when many outcomes, groups, or timepoints are examined. This is a general concern, not evidence that a particular procedure was or was not used. The posted p-values are unadjusted, and the record does not report multiplicity-adjusted estimates or thresholds.

The primary outcome includes comparisons of Treatment B and Treatment C with Treatment A. The record does not explain whether these were the only planned comparisons, whether other contrasts were planned, or how the primary question was defined before results were collected. Without that information, the degree to which the posted comparisons reflect a prespecified analysis cannot be assessed. The secondary outcome adds another endpoint, but no family of hypotheses or hierarchy is reported.

Missing-data handling is also not reported in the registry record. The posted arm sizes identify the participants included in the summaries, but they do not show whether all randomized participants contributed outcome data, why any measurements might be absent, or how missing values were treated. No imputation method, complete-case rule, or sensitivity analysis is described. These details matter because missingness can affect both the estimated group means and their uncertainty.

The record does not identify the analysis population, such as whether results were analyzed according to original random assignment or only among participants who completed treatment. Nor does it report protocol deviations, adherence, or exclusions after randomization. The registry status is terminated, but the reason for termination is not reported. Termination alone does not establish whether the study stopped early for a statistical, administrative, recruitment, or other reason.

For the secondary outcome, the registry record also does not define the maintenance criterion. Without that definition, it is not possible to evaluate classification of participants or determine whether the binary outcome was measured consistently. Taken together, the absent analysis, missing-data, and multiplicity details make the posted comparisons useful as descriptive summaries but limit a complete appraisal of inferential reliability.

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 3% reporting threshold.

Most frequent non-serious adverse event terms

The registry record reports zero serious adverse events among participants at risk in each of the three treatment arms and both maintenance arms. The arm-specific numbers at risk are 24 for Treatment A, 24 for Treatment B, 23 for Treatment C, 32 for Maintenance A, and 31 for Maintenance B. No serious adverse-event terms are listed. The record does not give a definition of serious adverse events or describe the period over which events were collected.

Zero reported serious events in these groups is a description of the posted safety counts. It does not establish that serious events could not occur, nor does it determine how well the study could detect uncommon events. The registry record does not report death counts. It also does not provide enough detail to assess completeness of event ascertainment or whether safety monitoring differed across the treatment and maintenance groups.

Other adverse events are listed separately from serious adverse events. Their counts should not be conflated with the serious-event figures, since the categories have different meanings. Safety summaries are descriptive; the registry record does not provide a comparative safety analysis or a reported statistical method for evaluating differences between arms.

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

The primary result describes group differences in a serum measure after 6 weeks. The mean change was higher in each active comparison arm than in Treatment A, and the posted confidence intervals for both mean differences are above zero. This supports a narrow statistical interpretation: the observed treatment groups differed in the posted 25OHD outcome over the stated timeframe.

That result does not by itself establish improvement in bone health or reduction in IBD activity. Serum 25OHD is described in the registry as reflecting vitamin D stores. It is not a direct measure of bone density, fractures, inflammation, symptoms, or disease course. The study rationale refers to those wider concerns, but a rationale is not a result. The registry record does not provide posted primary outcome estimates for those clinical outcomes.

The comparisons also do not establish a preferred regimen for every patient or setting. The record does not report eligibility criteria in detail, baseline characteristics, adherence, or an analysis plan. The trial is randomized and parallel, but the record lacks information needed to judge all aspects of conduct and analysis. Its listed open-label status is another feature to consider, although the primary outcome is a laboratory measurement and blinding of outcome assessment is not reported.

The maintenance result is distinct from the six-week treatment result. Its definition is incomplete in the record, and it cannot resolve whether the short-term differences persist or translate into clinical outcomes. More generally, one trial's posted summaries do not settle questions about longer-term effects, different populations, or outcomes not reported in the registry.

The most defensible conclusion is therefore limited to the posted data: the group means for serum 25OHD change differed at 6 weeks, with intervals that quantify sampling uncertainty under unreported methods. The clinical significance, durability, and implications for bone health or IBD outcomes are not established by these summaries.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it pairs a continuous primary measure with a separate participant-count maintenance outcome. The two outcome types require different ways of expressing comparisons and uncertainty. Mean differences in serum 25OHD are stated in the measurement's original units, while the secondary comparison is expressed as a risk difference and also includes relative measures. Keeping these estimands distinct prevents a short-term mean change from being mistaken for a long-term maintenance result.

The primary comparisons also illustrate why effect size and precision should be read together. The posted estimates have confidence intervals, so readers can assess a range of values compatible with the data under the calculation method. The p-values alone would not describe the magnitude of the differences or the uncertainty around them. Conversely, a measured difference in a biomarker does not automatically indicate an important clinical effect.

The record highlights the limits of registry summaries when analysis details are absent. It reports random allocation and arm-level outcomes, but does not report the statistical plan, analysis population, missing-data approach, or multiplicity strategy. Those omissions are relevant to interpretation even when the numerical comparisons appear clear. They also show why registrations and posted results should be considered alongside full trial methods when available; the record does not identify a publication.

Finally, the planning illustrations demonstrate how sample-size requirements depend on the effect chosen for detection. Smaller assumed effects require more participants under the stated assumptions. Because the illustrations are based on observed effects rather than the trial's documented original design, they should not be confused with evidence about the study's design quality or realized power. The distinction between planning and observed results is central to sound statistical interpretation.

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.

Several trial-specific limitations follow from the information absent in the registry record. The reason the study was terminated is not reported, and the record does not indicate whether termination affected recruitment, follow-up, or outcome availability. The overall enrollment is recorded as 134, while the posted treatment and maintenance groups have their own arm sizes; the record does not explain the relationship between those groups or whether any participants were represented at more than one stage.

The treatment and maintenance regimens differ in dose, formulation, and timeframe. Because the record does not clarify whether the groups were sequential or separate, the maintenance comparison cannot be interpreted as a continuation of a particular treatment-arm comparison. The maintenance outcome is also recorded at 12 months despite regimens described over 2 years, and the record does not explain that timing in greater detail.

The primary outcome is described as change in serum 25OHD, but the exact change calculation and baseline measurement details are not reported. The registry also does not provide baseline group characteristics, eligibility criteria, adherence, or missing-data handling. These omissions restrict assessment of group comparability, outcome completeness, and the practical meaning of the observed summaries.

The secondary endpoint's definition is not reported, and no analysis plan or multiplicity procedure is available. The study is listed as open-label, while blinding of outcome assessment is not reported. These limitations do not erase the posted results, but they narrow the conclusions that can be drawn and make it difficult to assess whether the reported comparisons fully reflect the intended trial analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Vitamin D Levels in Children With IBD — NCT00621257.
• Registry record last updated 2017-03-22; status last verified 2017-02.
• Results first posted 2017-02-17.
• 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

NCT00621257 is a randomized, parallel, open-label trial sponsored by Boston Children's Hospital and listed as terminated. Enrollment was 134. The primary outcome was change in serum 25OHD after 6 weeks among pediatric patients with inflammatory bowel disease. Three treatment arms compared ergocalciferol and cholecalciferol regimens, with Treatment A designated as control.

The posted primary means were 9.3, 16.4, and 25.4 ng/ml for Treatment A, Treatment B, and Treatment C. Mean differences versus Treatment A were 7.1 and 16.1 ng/ml, with unadjusted p-values of <0.001. The record also lists a 12-month maintenance outcome in two maintenance arms, but does not define the outcome criterion or explain how maintenance participants relate to the treatment groups.

The record does not report the original sample-size justification, statistical analysis plan, missing-data approach, or reason for termination. The primary data describe differences in a serum measure; clinical effects on bone health and IBD outcomes are not established by that measure alone.