Long-term Effects of Thalidomide for Recurrent Gastrointestinal Bleeding Due to Vascular Malformation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long-term Effects of Thalidomide for Recurrent Gastrointestinal Bleeding Due to Vascular Malformation (NCT00964496), a randomized phase 2 study. The primary outcome is Participants Whose Rebleeds Decreased From Baseline by ≥ 50% at 12 Months.

2. Clinical Question

The question focuses on a defined change in recurrent bleeding rather than simply whether any bleeding occurred. The registry describes rebleeding as a positive fecal occult blood test using monoclonal colloidal gold color technology. The endpoint compares the bleeding experience at 12 months with baseline, described as the year before randomization. It therefore combines a threshold for reduction in rebleeding with an assessment based on the specified test.

The main posted comparison is the proportion meeting that endpoint in the thalidomide and iron-controlled groups. It is a binary outcome: each participant either met the stated endpoint or did not. The registry also describes secondary measures related to hemoglobin, bleeding episodes, bleeding duration and transfusion requirements. Those measures add information about other aspects of bleeding and its consequences, but they do not replace the primary question.

3. Trial Design

The registry identifies this as a randomized, parallel controlled phase 2 study with no masking. It was open-label, so the registry does not describe participants or study staff as blinded to treatment assignment. The record lists an enrollment of 55 and status as completed. The start is recorded as 2004-11 and primary completion as 2007-11.

Participants with at least six bleeding episodes in the prior year due to vascular malformation were randomly grouped. One group received an oral four-month regimen of thalidomide, specified as 25 mg four times daily; the other received an oral four-month regimen of iron, specified as 100 mg four times daily. The brief summary says participants were monitored for at least one year. The registry record does not report the details of sequence generation, allocation concealment, adherence monitoring or the timing and frequency of follow-up visits.

The primary endpoint was assessed at 12 months and concerned a reduction in rebleeding from baseline by at least 50%. Rebleeding was defined using a positive fecal occult blood test at any visit after treatment. The record also lists secondary outcomes for change in hemoglobin, bleeding episodes and bleeding duration at 12 months, along with transfusion dependence and transfused red cell requirements.

The group results list 28 participants in the thalidomide group and 27 in the iron-controlled group. These are the denominators shown for the primary result. The registry record does not report a detailed participant flow, withdrawals, exclusions from analysis, or the number contributing data to each secondary outcome. It also does not report the original sample-size justification or the trial's prespecified statistical analysis plan.

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: Among the 59 patients, two refused to enter the protocol and two other were excluded owing to severe associated disease with short life expectancy. Therefore, 55 patients were enrolled in our study.

Overall Study

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 Participants Whose Rebleeds Decreased From Baseline by ≥ 50% at 12 Months, measured over baseline and 12 months.

The primary endpoint measures whether a participant's rebleeding decreased from baseline by at least 50% at 12 months. The registry describes baseline as the year before randomization and defines rebleeding as a positive fecal occult blood test at any visit after treatment. The outcome is reported as a count of participants meeting the endpoint in each group, so the comparison is between proportions rather than between average bleeding counts.

A threshold-based outcome can make a continuous or repeated clinical experience easier to interpret as a yes-or-no event. It captures whether a substantial reduction was achieved, according to the study's stated cutoff. That convenience comes with a trade-off: participants just on opposite sides of the cutoff are classified differently even if their underlying experiences are similar, while participants with different degrees of reduction can be grouped together once they meet the threshold.

The endpoint is relevant to the trial's stated question because the study concerns recurrent bleeding, and the registry defines the outcome using a change from each participant's baseline. Interpretation depends on the completeness and consistency of the fecal occult blood testing and the handling of missing visits; those procedures are not reported in the registry record. The endpoint also does not, by itself, describe transfusion burden, hemoglobin or bleeding duration. Those are listed separately as secondary outcomes.

7. Results Posted in the Registry

• Thalidomide Group: 71.4% (20/28) versus 3.7% (1/27) on control; risk difference 67.7 percentage points (95% CI 49.5 to 85.9), risk ratio 19.29 (2.78–133.87); unadjusted two-proportion 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.

Change From Baseline in Hemoglobin (Hb) Level at 12 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:
  • Thalidomide Group: mean 3.06 versus -0.01 on control; difference 3.07 (95% CI 2.15 to 3.99), standardized effect d = 1.76; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Thalidomide Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Bleeding Episodes at 12 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:
  • Thalidomide Group: mean -9.36 versus 1.41 on control; difference -10.77 (95% CI -12.67 to -8.87), standardized effect d = -2.97; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Thalidomide Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Bleeding Duration at 12 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:
  • Thalidomide Group: mean 5.20 versus 0.80 on control; difference 4.40 (95% CI 2.18 to 6.62), standardized effect d = 1.06; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Thalidomide Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide context beyond the threshold-based primary endpoint. Across the three secondary comparisons with posted numerical results, the observed changes describe differences in hemoglobin, bleeding episodes and bleeding duration between groups. The group summaries show a positive hemoglobin change for thalidomide and a change close to zero for iron; the bleeding-episode changes move in opposite directions between groups. For bleeding duration, the summaries report positive changes in both groups. The endpoint label alone does not establish whether that direction represents a favorable or unfavorable change.

This broad pattern relates to the primary result in that both the primary endpoint and some secondary measures concern bleeding. The measures are not interchangeable, however. The primary outcome classifies participants according to a threshold for rebleeding reduction, while the secondary outcomes report group averages for changes. A pattern across different measures can add context, but it does not make each measure a replication of the primary result.

The registry lists additional secondary outcomes for transfusion dependence and total transfused red cell requirements, but numerical results for those outcomes are not reported in the registry record. Their absence limits how completely the secondary outcomes can describe transfusion burden.

The posted secondary p-values are unadjusted. When several outcomes are tested, the chance of at least one apparently notable result can rise. The registry record does not report a correction for multiple comparisons, a priority order among secondary outcomes, or a plan for interpreting them jointly. The secondary findings therefore carry less weight as confirmatory evidence than the designated primary result. They should be read as additional, potentially informative observations, while recognizing uncertainty from multiple testing, outcome measurement and the lack of detail about missing observations and analysis populations.

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

• Change From Baseline in Hemoglobin (Hb) Level at 12 Months
• Change From Baseline in Bleeding Episodes at 12 Months
• Change From Baseline in Bleeding Duration at 12 Months
• Participants Dependent on Blood Transfusions
• Change From Baseline in Total Transfused Red Cell Requirements at 12 Months

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary outcome is binary: participants either met the registry's criterion for a decrease in rebleeding by at least 50% at 12 months or did not. A difference in proportions expresses the contrast between the share meeting the endpoint in the thalidomide group and the share in the iron-controlled group. The registry reports a difference in proportions of 0.677. A positive difference means the observed proportion meeting the endpoint was greater in the thalidomide group under the comparison's group order.

As a general statistical explanation, an absolute difference in proportions is often easier to read as a contrast in event frequency than a ratio. It does not, however, convey how outcomes vary among individual participants, and it does not describe events beyond the binary endpoint. It also depends on the definition of the event, including the fecal occult blood test rule and the 50% threshold.

Why use a Fisher exact test?

The registry identifies Fisher Exact as the method for the reported primary comparison. As a general explanation, Fisher's exact test evaluates evidence of association in a contingency table and can be used when event counts are sparse. Here the registry reports 1 participant meeting the endpoint in the iron-controlled group, so a method designed for categorical counts is pertinent to the form of the data. The test produces a p-value under a null hypothesis of no group association; it does not measure the size of the difference or the chance that the null hypothesis is true.

The reported p-value is below 0.001. The registry summary defines statistical significance at P < 0.05. A small p-value indicates that data at least as incompatible with the null hypothesis would be unusual under the test's assumptions if there were no group association. It does not address bias, missing outcomes, the correctness of endpoint measurement, or whether other outcomes show the same pattern.

What does an unadjusted recalculation mean?

The recalculated binary comparison uses the posted group counts and denominators to form a simple, unadjusted contrast. It is not a substitute for a prespecified model or a fuller analysis of individual participant data. For continuous secondary outcomes, recalculations use the posted group means and standard deviations to estimate unadjusted mean differences. These calculations do not adjust for baseline covariates or other factors. The registry record does not report an adjusted model for the posted comparisons.

For continuous outcomes, the standard deviation describes how spread out participant measurements are around a group mean. A mean difference compares the group averages, but it can conceal variation and skew in the underlying observations. General statistical methods may use models or transformations when data are not well represented by a normal distribution; the registry record does not report such additional methods for these secondary results.

How should the secondary p-values be read?

The posted secondary analyses use two-sided t-tests for mean differences in final values. A two-sided test considers departures in either direction rather than testing only one prespecified direction. The registry lists p-values for the posted secondary analyses, but does not report a multiplicity correction or a hierarchical testing procedure. As a general statistical point, examining multiple outcomes creates more opportunities for apparently small p-values, even if each individual test uses the same threshold. The results are therefore best treated as supportive or exploratory rather than as independent confirmatory findings.

The reported secondary analyses describe mean differences in final values, while the posted outcome summaries also give changes from baseline. These are different quantities, and their estimates need not have the same direction or magnitude. Baseline levels can affect comparisons of final values, whereas a change score incorporates the baseline measurement. The registry record does not provide enough detail about the analysis plan to determine how this distinction was addressed in the original analysis.

What is not described about the analysis?

The registry record does not report the randomization sequence method, allocation concealment, the analysis population, a missing-data method, or whether participants were analyzed according to their randomized group. It also does not report a sample-size justification, interim analyses, or a full statistical analysis plan. These are not details that can be inferred from the posted p-values or confidence intervals. Their absence limits assessment of whether the reported analyses followed a prospectively specified plan and how robust the results are to incomplete data or analytic choices.

11. Confidence Intervals and Precision

The registry reports a 95% confidence interval from 0.547 to 0.807 for the primary difference in proportions, whose point estimate is 0.677. The interval gives a range of values compatible with the observed data and the method's assumptions. It communicates uncertainty about the estimated group difference; it is not a range that contains 95% of individual participant outcomes, nor does it assign a 95% probability to a fixed effect being inside the interval.

The reported interval lies on the positive side of no difference, consistent with the reported p-value below 0.001. Its width also matters: it shows that the point estimate should not be treated as exact. A confidence interval is more informative than a p-value alone because it conveys both the direction and a range of plausible effect sizes under the analysis. The range remains conditional on how the endpoint was defined and on the validity of the underlying measurements and analysis.

For the primary comparison, the registry reports the sponsor's estimate and interval, and the unadjusted recalculation is also based on the posted group counts. Small groups mean that each participant's endpoint classification can affect the estimated proportions. The interval does not account for possible bias from open-label assessment, missing data, or outcome selection unless those features are incorporated in the analysis, which is not reported in the registry record.

Confidence intervals for the secondary comparisons likewise express uncertainty under their respective methods, but they should be considered in light of the number of outcomes examined and the unreported multiplicity approach. Precision is not the same as validity: a numerically narrow interval cannot correct systematic bias, and a statistically significant result does not eliminate uncertainty about the endpoint or its broader meaning.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculations. The tables and curve express the estimated participants needed per arm for the non-time-to-event outcomes; the registry's stated convention is that time-to-event displays would instead use total events, but the posted outcomes are not time-to-event measures. The assumptions for these illustrations 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 as the stated fraction of the observed effect.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions hold. The 90% power column gives the corresponding planning figure for a 90% chance. These are prospective planning quantities, not evidence about how likely the completed study was to detect an effect. This is not observed power.

Rows planning for 100% of the observed effect use the full observed effect as the target; rows planning for 75% or 50% use smaller target effects. Smaller effects generally require more participants to distinguish them from random variation at the same significance level and power. The values are sensitive to the observed effect used as the starting point, which may itself be unstable in a small study. They are therefore illustrations, not a recommendation or a substitute for a new design's assumptions and justification.

The registry record does not report the trial's own sample-size justification or original design assumptions. The posted planning figures should not be read as evidence that the study was originally sized to detect the observed effect, nor as a retrospective measure of whether the trial was adequate. The curve conveys the same planning relationship across effect assumptions; its interpretation is conditional on the stated illustration model.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.037; treatment proportion p₁ = 0.714; average p̄ = 0.376.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6849 = 1.3424.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4896 = 0.4121.
4. n = (1.3424 + 0.4121)² / (0.6772)² = 6.7, rounded up to 7 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.037037037037037                          # control proportion
p1 <- 0.714285714285714                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(964496)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 7 (80% power), 9 (90% power)
 75% of observed effect: n per arm = 12 (80% power), 15 (90% power)
 50% of observed effect: n per arm = 22 (80% power), 28 (90% power)
power.prop.test: 6.7 
Simulated power at n = 7 per arm: 0.838 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a Fisher exact analysis for the primary difference in proportions: an estimate of 0.677, a 95% confidence interval from 0.547 to 0.807, and a p-value below 0.001. The unadjusted recalculation is based on the posted event counts and denominators and is intended as a simple check of the summary data, not a replacement for the reported analysis. Both indicate a larger observed proportion meeting the primary criterion in the thalidomide group.

For the secondary outcomes, the registry's reported analyses are described as two-sided t-tests of mean differences in final values. The recalculations use the posted change-from-baseline means and standard deviations. A comparison of final values is not identical to a comparison of changes, so the corresponding estimates can differ in direction or magnitude without representing the same estimand. The registry record does not report enough of the analysis plan to reconcile every difference between these approaches.

The discrepancy indicator does not flag a discrepancy. Where a posted recalculation and a sponsor analysis genuinely conflict, the sponsor's own analysis takes precedence. These recalculations should remain transparent, unadjusted checks of the posted summaries, with no implication that they reproduce an individual-level analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and multiple secondary outcomes. It states that statistical significance was defined at P < 0.05, but does not report whether that threshold was adjusted for multiple testing. A multiplicity adjustment, a prespecified sequence of tests, or another strategy for controlling false-positive findings is not reported in the registry record. Without such information, the secondary p-values should not be treated as if each were an isolated confirmatory test with no selection issue.

The record does not report how missing primary or secondary measurements were handled, whether any participants were excluded from an analysis, or the analysis population used. It also does not give a detailed account of withdrawals, losses to follow-up, protocol deviations or outcome availability by group. The monitoring period is described as at least one year, but that does not by itself establish that every participant contributed complete 12-month data.

Random assignment is reported, but the sequence generation and allocation concealment procedures are not. Masking is listed as none, so participants and study personnel were not described as blinded. The record does not explain whether outcome assessors were separately masked. These reporting gaps do not show that a particular procedure was absent; they mean the registry record does not describe it.

The registry also does not report interim analyses, stopping rules, a full statistical analysis plan or the original sample-size justification. These details are important for assessing whether the endpoint, analysis choices and stopping decisions were set in advance. No inference about those procedures can be made from the reported results alone.

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 2% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record lists 0 serious adverse events in the thalidomide group among 28 at risk and 0 in the iron-controlled group among 27 at risk. It lists other, non-serious adverse events affecting 20 participants in the thalidomide group and 9 in the iron-controlled group. No serious adverse-event terms are listed.

These counts describe what the registry record reports during the study; they do not establish that serious events are impossible or that the groups have equal safety profiles. A zero count in a study of this size leaves uncertainty about uncommon events, and the record does not provide event-level detail, severity classifications for the other events, or timing. The death counts are not reported in the registry record.

The adverse-event figures should be kept separate from the efficacy endpoint. They do not explain the primary comparison or establish a benefit-risk balance. The registry record also does not provide enough information to assess how adverse events were collected, attributed or followed after treatment.

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

The primary data show that a larger observed proportion of participants in the thalidomide group met the registry's definition of a decrease in rebleeding by at least 50% at 12 months than in the iron-controlled group. The reported difference in proportions is 0.677, with a 95% confidence interval from 0.547 to 0.807. The result is statistically distinguishable from no difference under the reported Fisher exact analysis, but its interpretation remains tied to this study's endpoint, participants and follow-up.

The result does not mean that every participant in the thalidomide group had the same experience, or that no participant in the iron-controlled group improved. It does not describe the full distribution of bleeding episodes, transfusions, hemoglobin or other outcomes. The registry's primary endpoint uses a threshold, and the secondary measures address different aspects of the condition.

The result also does not by itself establish how well the finding applies to people outside the study population. The record describes participants with at least six bleeding episodes in the prior year due to vascular malformation. The registry record does not report detailed eligibility criteria beyond that summary, the analysis population, missing-data handling or longer-term outcomes beyond the stated monitoring description.

Open-label assignment and the absence of reported detail on outcome assessment leave uncertainty about possible measurement or performance effects. Randomization supports a group comparison, but it does not remove every source of bias, particularly when reporting on trial conduct and analysis is limited. The confidence interval quantifies sampling uncertainty under the analysis; it does not account automatically for all design and reporting limitations.

Accordingly, the posted result is an estimate from this randomized study, not a guarantee of an individual outcome or a complete evaluation of all benefits and harms. The registry record provides useful evidence about the measured endpoint while leaving important questions about outcome completeness, secondary results and study procedures unresolved.

18. Why This Trial Matters Statistically

This trial illustrates how endpoint definition shapes a treatment comparison. The primary result is not simply a count of bleeding episodes or a measure of whether bleeding stopped. It is a binary classification based on a specified reduction from baseline, at a defined follow-up, with rebleeding identified through a fecal occult blood test. Statistical interpretation depends on understanding that operational definition before considering the p-value or confidence interval.

It also shows why effect estimates and uncertainty should be read together. The reported difference in proportions communicates the size and direction of the observed contrast, while the confidence interval shows that the estimate is not exact. A small p-value addresses compatibility with a null comparison under a test; it does not describe precision, individual outcomes or the possibility of bias.

The study offers an example of the distinction between a prespecified primary outcome and a group of secondary measures. Secondary measures can deepen interpretation, but multiple unadjusted tests and incomplete reporting limit their confirmatory force. The registry's secondary endpoints include clinically relevant domains, yet some listed measures have no numerical results in the record.

Finally, the record demonstrates the value of reporting design and analysis details. Randomization and group counts are documented, but important information about missing data, analysis populations, allocation procedures and sample-size planning is not. Such omissions constrain appraisal even when a primary comparison is statistically strong. For biostatisticians and clinical researchers, the lesson is to connect numerical results to the estimand, the measurement process, design transparency and the limits of the registry record.

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 principal limitation is the small size of the reported groups, which makes the primary estimate sensitive to the endpoint classification of individual participants. The confidence interval communicates sampling uncertainty, but cannot address bias arising from design or conduct. The study was open-label, and the registry does not report whether outcome assessors were masked.

The endpoint depends on a threshold of at least 50% reduction and on fecal occult blood testing at visits after treatment. The registry record does not detail test schedules, adherence to testing, adjudication, or how missing visits and test results were handled. Nor does it report the analysis population or participant flow, so the completeness of 12-month outcome data cannot be assessed from the record.

Several aspects of trial conduct and analysis are not described, including the randomization sequence, allocation concealment, a full statistical analysis plan, the original sample-size justification and any interim analyses. The record does not report a multiplicity strategy for secondary outcomes. Numerical results are posted for three secondary measures, while results for the listed transfusion outcomes are not reported in the registry record. Death counts are also not reported.

These limitations concern reporting and the scope of the available evidence. They do not establish that a specific method was not used or that the posted results are invalid. They do mean that the primary estimate should be interpreted with attention to uncertainty and that broader conclusions cannot be drawn from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Long-term Effects of Thalidomide for Recurrent Gastrointestinal Bleeding Due to Vascular Malformation — NCT00964496.
• Registry record last updated 2015-12-17; status last verified 2009-08.
• Results first posted 2010-04-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed randomized, open-label, parallel controlled phase 2 study of thalidomide versus iron for recurrent gastrointestinal bleeding due to vascular malformation. Enrollment is listed as 55. Participants had at least six bleeding episodes in the prior year and were prescribed four-month oral regimens; monitoring was described as lasting at least one year.

The primary endpoint was a decrease in rebleeding from baseline by at least 50% at 12 months, with rebleeding defined by a positive fecal occult blood test. The posted primary comparison reports 20 of 28 participants meeting the endpoint in the thalidomide group and 1 of 27 in the iron-controlled group. The reported difference in proportions is 0.677, with a 95% confidence interval from 0.547 to 0.807 and a p-value below 0.001.

Secondary numerical results are posted for hemoglobin, bleeding episodes and bleeding duration. The registry record does not report numerical results for the listed transfusion outcomes, missing-data handling, analysis populations or the original sample-size justification.