Iodixanol Versus Iopamidol in Patients Undergoing Contrast-Enhanced Computed Tomographic Imaging of Abdomen/Pelvis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Iodixanol Versus Iopamidol in Patients Undergoing Contrast-Enhanced Computed Tomographic Imaging of Abdomen/Pelvis (NCT01376089), a randomized phase 4 study. The primary outcome is Frequency of Subjects With Moderate/Severe Discomfort When Undergoing Contrast-Enhanced Computed Tomographic (CECT) Imaging of the Abdomen/Pelvis..

2. Clinical Question

The clinical question is whether the frequency of reported moderate or severe discomfort differed between patients assigned to iodixanol and patients assigned to iopamidol during contrast-enhanced computed tomographic imaging of the abdomen and pelvis. Discomfort was defined for cold, heat, or pain and measured within 10 minutes after contrast administration. The registry describes the study as comparing patient comfort and safety.

This framing keeps the outcome tied to the registry’s stated measure: the number of subjects meeting the discomfort definition during a specified short period. It is not a general measure of comfort at other times, nor does it address every aspect of imaging experience. The registry also lists overall image quality as a secondary outcome, but numerical results for that outcome are not reported in the registry record.

3. Trial Design

The registry identifies this as a phase 4 randomized, double-blind, parallel-group study sponsored by GE Healthcare. The study compared iodixanol 320 mg I/mL with iopamidol 370 mg I/mL in patients undergoing contrast-enhanced CT imaging of the abdomen and pelvis. The recorded enrollment is 304. The registry describes the study as completed, with a start date of 2011-05 and primary completion in 2011-10.

Random allocation is relevant because, in principle, it aims to make the groups comparable at the start of a trial. Double blinding is intended to limit the influence of treatment knowledge on participant experience, reporting, or assessment. The registry records those design features, but does not give further detail about how allocation was generated or concealed, who was blinded, or how blinding was maintained. Those procedural details are not reported in the registry record.

The registry lists one arm for iodixanol and one for iopamidol. For the primary discomfort outcome, it reports 53 subjects with discomfort among 151 in the iodixanol arm and 99 among 147 in the iopamidol arm. The at-risk group sizes in the adverse-event record differ: 151 for iodixanol and 148 for iopamidol. The registry does not explain the difference between the outcome denominators and the safety denominators.

The primary outcome concerns moderate or severe discomfort within 10 minutes after contrast administration. An image-quality comparison is listed as a secondary outcome. The record states that there are 3 outcome measures and 0 analyses, and gives no numerical results for image quality. Further information on eligibility, the recruitment setting, participant flow, protocol deviations, and the analysis populations is not reported in the registry record. These omissions limit how fully the conduct and analysis of the trial can be reconstructed from the registry entry alone.

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: A total of 304 subjects were enrolled in this study, however, 5 subjects did not receive contrast media due to administrative and /or technical reason leaving 299 subjects included in the analysis.

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 Frequency of Subjects With Moderate/Severe Discomfort When Undergoing Contrast-Enhanced Computed Tomographic (CECT) Imaging of the Abdomen/Pelvis., measured over Within 10 minutes post contrast administration.

The primary endpoint counts subjects who experienced any moderate or severe discomfort related to cold, heat, or pain during contrast-enhanced CT imaging. The registry defines moderate discomfort as a score of 4 - 7 and severe discomfort as a score of 8 - 10. The assessment window is within 10 minutes after contrast administration. The posted outcome is a number of subjects, rather than a continuous comfort score or a time-to-event measure.

A binary endpoint such as this is useful when the study question concerns whether each subject crossed a prespecified threshold for an event. It produces an event count and a denominator for each arm, which can then be compared as risks or as a difference in risks. Those summaries are interpretable as frequencies of subjects meeting the endpoint definition. They do not retain all the detail of a graded symptom scale: a subject just meeting the threshold and a subject with a higher score both contribute as an event.

The endpoint therefore addresses a focused aspect of immediate patient experience. Its definition joins cold, heat, and pain into one outcome and combines moderate and severe scores. The registry does not report separate counts for each sensation or severity level, nor does it report further details of the instrument, assessor, or handling of incomplete symptom assessments. The listed result should be read as the combined endpoint that the registry defines, not as evidence about every component considered separately.

The short assessment window makes the result specific to discomfort soon after contrast administration. It does not describe symptoms outside that window or image quality. The latter is listed as a secondary outcome, but its numerical findings are not reported in the registry record.

7. Results Posted in the Registry

• Arm 2-Iopamidol (Isovue): 67.3% (99/147) versus 35.1% (53/151) on control; risk difference 32.2 percentage points (95% CI 21.5 to 43.0), risk ratio 1.92 (1.50–2.45); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary endpoint, each subject is classified as having or not having the event according to the stated definition. Here, the event is moderate or severe discomfort from cold, heat, or pain within 10 minutes after contrast administration. The registry reports event counts and outcome denominators for each arm. The corresponding arm risks are represented in the record, along with a comparison between the arms.

What does a risk comparison describe?

A risk is the frequency of subjects with the event among those included in the relevant group. A risk difference expresses the absolute contrast between two such risks. It is distinct from a risk ratio, which compares them multiplicatively, and from an odds ratio, which compares event odds. These measures answer related but not identical questions. The posted comparison is labelled as a risk difference. Other measures should not be substituted for it when describing the primary result.

Absolute contrasts are often straightforward to interpret because they retain the scale of event frequency. Relative measures can make proportional contrasts easier to compare across settings, but may sound large or small without the underlying risks. The registry includes risk-related comparison fields, but the main interpretation remains anchored to the event counts, group denominators, and reported direction of the primary comparison. No new contrast is calculated from those figures.

Why use a confidence interval?

A confidence interval describes the statistical uncertainty around an estimated quantity under the method used to construct it. A narrower interval indicates greater precision, while a wider interval indicates greater uncertainty. The interval is not a guarantee that the true effect lies within its limits, and it does not account automatically for every source of uncertainty, such as bias, missing information, or differences between the trial population and another population.

The registry supplies arm-level lower and upper limits and comparison-level limits. It does not report the confidence level or the interval calculation method. Consequently, the limits can be described as the intervals recorded for the outcomes, but the particular coverage interpretation and assumptions behind them cannot be verified from the registry record alone. The posted p-value and interval information should be considered together rather than treating either as a complete account of the evidence.

What does the p-value add?

The unadjusted p-value evaluates the observed contrast against a null model of no difference, subject to the statistical test’s assumptions. A small p-value means that data at least as incompatible with that null model would be relatively unusual if the model and assumptions were correct. It does not tell readers the probability that chance alone caused the observed result, and it does not quantify the clinical importance of the difference.

“Unadjusted” matters because a study can assess more than one outcome or make more than one comparison. When many hypotheses are tested, the chance of at least one small p-value can rise. The registry lists a secondary image-quality outcome and records 3 outcome measures, but does not report a multiplicity plan. The reported primary p-value should therefore be understood as posted, unadjusted evidence; the registry record does not establish whether or how the full outcome family was accounted for.

How does randomization affect interpretation?

Random assignment is intended to distribute measured and unmeasured participant characteristics across groups on average, supporting a fair comparison. It does not ensure exact balance, and it cannot prevent bias arising after assignment. Blinding may reduce the influence of knowledge of treatment on symptom reporting or assessment, but the registry does not provide enough procedural detail to assess its success. The randomized, double-blind labels are relevant design information, not proof that every possible source of bias was removed.

The registry gives the outcome counts and denominators, but does not report a detailed analysis population, missing-data method, or participant-flow accounting. If some participants lacked outcome assessments, the way they were handled could affect the comparison. The posted record does not state whether missing observations occurred, so their presence or absence should not be assumed. Likewise, no adjusted model or covariate set is reported.

Why can event counts be less informative than the full scale?

Turning a graded symptom score into an event indicator makes the outcome easy to summarize and compare, but it discards distinctions within each category. The threshold determines who counts as an event, so the result depends on the stated cut points. In this trial, the registry combines cold, heat, and pain and combines moderate and severe discomfort. The aggregate counts cannot reveal which sensation or severity category accounts for the contrast. Separate component results are not reported in the registry record.

For binary outcomes, statistical methods generally model the event probability or compare observed event frequencies. The validity and precision of a method depend on its assumptions, including how the data are sampled and how the comparison is specified. The registry identifies the posted comparison as a risk difference, but does not describe the inferential procedure used for its estimate, interval, or p-value. Those details should not be inferred from the numerical output alone.

The record also provides planning illustrations based on the observed effect, with a two-sided significance level of 0.05, equal allocation, and a normal approximation. Those are planning calculations, not descriptions of the trial’s own design rationale or analysis procedure. The original sample-size assumptions and the trial’s statistical analysis plan are not reported in the registry record.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated outcome or comparison. The registry records arm-level interval limits of 27.49 to 42.71 for iodixanol and 59.77 to 74.93 for iopamidol. These limits are listed alongside the arm event counts and denominators. The registry does not state the confidence level or method used for these intervals, so their exact coverage interpretation cannot be confirmed from the record.

The comparison also has an interval in the registry. In general, an interval around a difference expresses uncertainty about the estimated contrast: a range of values closer together suggests a more precise estimate, while a broader range reflects less precision. The interval should be considered alongside the direction of the estimate and the observed counts. It is not a range of individual subject outcomes, and it does not account on its own for potential bias, missing outcome data, or limitations in generalizability.

The posted p-value is unadjusted and is reported as p < 0.001. A small p-value and an interval are related summaries but are not interchangeable. The p-value addresses compatibility with a null hypothesis under a test; the interval conveys a range of uncertainty for an estimate under its construction method. Neither alone determines the practical importance of the finding.

Precision is also affected by the available information in each arm and by the number of recorded events. The registry does not provide enough methodological detail to assess all assumptions behind the interval calculations. It also does not report missing-data details, analysis populations, or confidence levels. Those omissions make it important to treat the interval limits as the posted statistical summaries rather than as a complete account of uncertainty.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They illustrate the number of participants that a hypothetical future comparison would require under the stated planning assumptions. The assumptions are a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is set at a stated fraction of the observed effect. The original trial’s sample-size rationale and design assumptions are not reported in the registry record.

The 80% power column gives the planned participants per arm for a calculation designed to have an 80% chance of detecting the selected effect under its assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are design targets under a statistical model, not guarantees that a study will detect an effect or that an observed finding is correct. This is not observed power.

The rows use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Under the stated setup, the planning numbers increase as the target effect becomes smaller: detecting a more modest contrast generally requires more information, often through more participants. The displayed figures are 37 and 49 participants per arm for planning around 100% of the observed effect; 66 and 88 per arm for 75%; and 147 and 197 per arm for 50%, with the first figure in each pair corresponding to 80% power and the second to 90% power.

These are illustrations anchored to the observed effect, so they should not be read as proof that the original trial was designed around those targets. They also rely on equal allocation and the other stated assumptions, which may not match every future study. A planning result changes if the chosen target effect, allocation, significance level, or statistical method changes. The figures describe participants per arm throughout; they are not numbers of total events.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.351; treatment proportion p₁ = 0.673; average p̄ = 0.512.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7069 = 1.3855.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6691 = 0.5631.
4. n = (1.3855 + 0.5631)² / (0.3225)² = 36.5, rounded up to 37 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 <- 0.350993377483444                          # control proportion
p1 <- 0.673469387755102                          # 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(1376089)
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 = 37 (80% power), 49 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 88 (90% power)
 50% of observed effect: n per arm = 147 (80% power), 197 (90% power)
power.prop.test: 36.5 
Simulated power at n = 37 per arm: 0.805 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy. Multiplicity arises when a study evaluates several outcomes, comparisons, time points, or subgroups. Repeated testing can increase the chance of obtaining at least one apparently strong result even when no true effect exists. Statistical plans may address this through a prespecified hierarchy or adjustment, but neither approach is documented in the registry record for this study. The primary comparison is reported with an unadjusted p-value.

The registry lists one secondary outcome concerning overall image quality and records 3 outcome measures. Numerical results for the image-quality outcome are not reported in the registry record. The record reports 0 analyses. It therefore does not provide a full set of results from which to assess how outcomes were selected, whether additional comparisons were made, or how a family of tests was handled.

Missing-data handling is also not reported in the registry record. The posted primary outcome has denominators of 151 for iodixanol and 147 for iopamidol, while the safety record has at-risk denominators of 151 and 148. The reason for the difference is not stated. No conclusion about missingness, exclusions, or participant flow should be drawn from the denominator difference alone. The record does not describe whether the analysis included all randomized participants or used another population definition.

Details of imputation, complete-case analysis, sensitivity analyses, and treatment of protocol deviations are not reported in the registry record. Nor does the record describe an adjusted model or covariates. These omissions mean that the posted result can be read as the registry’s stated comparison, but the robustness of that result to alternate data-handling or analysis choices cannot be assessed from the entry alone. The registry’s randomized and double-blind design labels do not replace a documented analysis plan.

14. 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: acute appendicitis (0.7%).

The registry reports serious adverse events for groups with 151 subjects at risk in the iodixanol arm and 148 at risk in the iopamidol arm. It records 0 serious adverse events in the iodixanol group and 1 in the iopamidol group. Death counts are not reported in the registry record. Acute Appendicitis is listed among the top serious-event terms at 0.7%; the record does not identify an arm for that term in the listed information.

For other adverse events, the registry records 121 affected subjects among 151 at risk in the iodixanol arm and 134 among 148 at risk in the iopamidol arm. These are counts of subjects, not counts of every event occurrence. The registry does not provide event-level detail or explain the difference between the safety denominators and the primary-outcome denominators.

Rare serious events require cautious interpretation. A zero count in one group does not establish that an event is impossible, and a small count cannot by itself define comparative safety. These registry figures describe what was recorded for the listed categories and denominators; they do not establish causation or characterize all potential adverse effects. Further information about event definitions, follow-up, attribution, and missing safety data is not reported in the registry record.

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

The primary result describes a higher recorded frequency of the combined moderate-or-severe discomfort endpoint in the iopamidol arm than in the iodixanol arm. The outcome counts are 99 of 147 for iopamidol and 53 of 151 for iodixanol, and the registry reports an unadjusted p < 0.001 for the comparison. These figures apply to the trial’s stated symptom definition and assessment window: cold, heat, or pain within 10 minutes after contrast administration.

This result does not answer every question about contrast-enhanced CT. The endpoint combines several sensations and severity levels, so the aggregate comparison cannot identify which sensation or score category accounts for the difference. It also does not describe comfort outside the assessment window. Overall image quality is listed as a secondary outcome, but numerical results are not reported in the registry record.

The result does not show that every patient in one arm experienced discomfort or that no patient in the other arm did. It is a group-level comparison of recorded events. Nor does a p-value establish the probability that the finding is true, quantify its importance to patients, or explain its cause. The registry’s randomization and double-blind labels are useful design information, but details needed to evaluate allocation, blinding, missing data, and analysis populations are not reported in the registry record.

The posted data also do not establish how the result would translate to settings, populations, or procedures beyond the study’s abdominal/pelvic contrast-enhanced CT context. The registry does not provide subgroup findings or numerical image-quality findings. The safety counts should be interpreted separately from the discomfort result: they are recorded adverse-event summaries with different at-risk denominators and do not, by themselves, settle comparative safety.

In statistical terms, the registry supports describing a difference in the observed frequency of its defined primary endpoint, with the reported unadjusted test result. It does not support a broader claim about all aspects of patient experience, image quality, or safety, and it does not prescribe a treatment choice. Those questions require evidence and context beyond the posted registry outcomes.

16. Why This Trial Matters Statistically

This trial illustrates how a patient-experience outcome can be made statistically tractable by defining a symptom threshold and a time window. The registry counts subjects who crossed the stated moderate-or-severe threshold for cold, heat, or pain within 10 minutes after administration. That concise endpoint allows a between-arm comparison of event frequencies, while also compressing symptom and severity detail into a single binary result.

It also shows why the effect measure and its uncertainty matter. A count alone cannot be compared fairly without considering the group denominator. A p-value alone cannot communicate the size or precision of a contrast. The registry provides counts, denominators, a risk-difference comparison, interval limits, and an unadjusted p-value; these are complementary ways to describe the same primary outcome. Each has limitations, particularly when the interval method and confidence level are not described.

The record highlights the distinction between an observed result and a planning assumption. The sample-size illustrations use fractions of the observed effect under stated statistical assumptions. They show how planning requirements change when the target effect is smaller, but they do not explain the original trial’s design or establish its power. The registry’s original sample-size rationale is not reported in the registry record.

Finally, the entry is a reminder that trial design labels do not answer every methodological question. Randomization and double blinding are important features, but readers also need information on analysis populations, missing data, multiplicity, outcome reporting, and safety follow-up. Several of those details are not reported in the registry record. Recognizing both the strength of the posted comparison and the limits of the record is central to sound statistical interpretation.

17. 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 registry record leaves important details unavailable for evaluating the conduct and analysis. It does not report the eligibility criteria, participant characteristics, recruitment setting, randomization procedure, allocation concealment, or which parties were blinded. Although the study is identified as randomized and double-blind, the record does not describe how those safeguards operated or whether blinding was maintained.

The primary outcome combines cold, heat, and pain and groups moderate and severe scores together. Separate component counts and the distribution of symptom scores are not reported in the registry record. This prevents assessment of whether the aggregate result is driven by one sensation or one severity level. The record also does not give further information about the assessment instrument or who assessed the outcome.

Analysis details are limited. The record does not report the statistical test, interval method or confidence level, analysis population, covariate adjustment, missing-data handling, or sensitivity analyses. It records an unadjusted p-value but does not describe a multiplicity plan. The secondary image-quality outcome is listed without numerical results, and the registry records 0 analyses.

The primary outcome denominators and the safety at-risk denominators differ for the iopamidol arm, with no explanation in the registry record. The entry does not provide participant flow or explain exclusions, if any. Death counts are not reported, and the serious adverse-event information is limited to the posted counts and term listing. These limitations mean the registry results can be described, but several questions about completeness, robustness, and generalizability remain unresolved.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Iodixanol Versus Iopamidol in Patients Undergoing Contrast-Enhanced Computed Tomographic Imaging of Abdomen/Pelvis — NCT01376089.
• Registry record last updated 2013-12-19; status last verified 2013-11.
• Results first posted 2013-12-19.
• 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.

21. Record Summary

NCT01376089 is a completed phase 4 randomized, double-blind, parallel-group study comparing iodixanol 320 mg I/mL with iopamidol 370 mg I/mL for contrast-enhanced CT imaging of the abdomen and pelvis. The registry records enrollment of 304 and identifies patient comfort and safety as the condition area.

The primary outcome counts subjects with moderate or severe discomfort from cold, heat, or pain within 10 minutes after contrast administration. The registry reports 53 events among 151 in the iodixanol arm and 99 among 147 in the iopamidol arm, with an unadjusted p < 0.001. Overall image quality is listed as a secondary outcome, but its numerical result is not reported in the registry record.

Safety summaries record 0 serious adverse events among 151 at risk for iodixanol and 1 among 148 at risk for iopamidol. The registry does not report death counts. Several methodological details, including missing-data handling, analysis populations, multiplicity, and the interval calculation methods, are not reported in the registry record.