Prevention of Serious Adverse Events Following Angiography: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prevention of Serious Adverse Events Following Angiography (NCT01467466), a randomized phase 3 study. The primary outcome is Number of Participants With Serious, Adverse, Patient-Centered Events, Including Death, Need for Acute Dialysis, or Persistent Decline in Kidney Function, Comparing Intravenous Sodium Bicarbonate With Intravenous Sodium Chloride..

2. Clinical Question

The primary question is about a composite endpoint, rather than a single event. Its components represent death, a need for renal replacement treatment, and a sustained change in kidney function as defined by the registry. Combining these outcomes gives one count for the principal comparison, while leaving the individual components with potentially different clinical meanings.

The record reports 111 participants with the endpoint among 2393 in the bicarbonate group and 116 among 2379 in the saline group. These are the posted counts for the intravenous-fluid comparison. They describe the observed results in the analyzed groups; they do not establish that one fluid caused a difference or that either treatment changes an individual participant’s outcome.

The factorial structure means the trial assigned participants across combinations of intravenous fluid and oral capsule. However, the primary outcome result reported in the record is specifically a comparison of bicarbonate with saline. The posted result does not provide a corresponding estimate for the oral N-acetylcysteine-versus-placebo question, nor does it report an interaction result for the two treatment factors.

3. Trial Design

The registry describes a Phase 3, randomized, double-masked, factorial trial sponsored by the VA Office of Research and Development. Its listed enrollment is 5177, and its status is completed. The recorded study start is 2013-10-07, and the primary completion date is 2017-09-29. These registry entries describe the trial’s design and record status; they do not by themselves establish how every participant was analyzed.

The factorial design crossed two treatment assignments: intravenous isotonic saline or intravenous isotonic bicarbonate, and oral placebo or oral N-acetylcysteine. The resulting combinations were saline with oral placebo, saline with oral N-acetylcysteine, bicarbonate with oral placebo, and bicarbonate with oral N-acetylcysteine. The registry identifies the study’s purpose as comparing both treatment factors for prevention of serious adverse outcomes following angiographic procedures in high-risk patients.

The primary outcome result pools the oral-capsule combinations to compare the intravenous fluids. In that comparison, the registry lists 2393 participants in the bicarbonate group and 2379 in the saline group. The primary event counts are 111 and 116, respectively. These group counts are not the same as a description of the four individual treatment combinations, and the posted primary estimate does not show a separate result for each combination.

Randomization is intended, in general, to make treatment groups comparable on average, while masking can reduce the influence of treatment knowledge on care or outcome assessment. Those are general design purposes, not evidence about how masking was maintained or whether it was successful in this trial. The exact allocation procedures, masking roles, and detailed randomization methods are not reported in the registry record.

The registry gives the trial status, dates, enrollment, arms, and primary comparison, but does not report the original sample-size justification or the protocol’s full statistical plan. In particular, the planned analysis populations, interim monitoring procedures, and prespecified handling of the factorial treatment combinations are not reported in the registry record. The registry’s displayed sample-size planning illustration is a calculation based on the observed effect, not a description of the trial’s original design assumptions.

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.

Population: A total of 5,177 participants were randomized into this trial. 4,993 participants completed baseline activities and summary information is provided below. A total of 4,772 participants were assessed for the primary outcome, which accounts for the discrepancy in numbers reported between baseline and outcome sections in this submission.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Serious, Adverse, Patient-Centered Events, Including Death, Need for Acute Dialysis, or Persistent Decline in Kidney Function, Comparing Intravenous Sodium Bicarbonate With Intravenous Sodium Chloride., measured over Within 90 days following angiography.

The primary endpoint counts participants who experienced at least one of three serious, patient-centered events within 90 days following angiography: death, need for acute dialysis, or persistent decline in kidney function. The record says death was based on medical records and/or vital status registry documentation. Acute dialysis was defined to include initiation of any modality of renal replacement, including intermittent hemodialysis, peritoneal dialysis, continuous renal replacement therapy, or sustained low-efficiency dialysis.

Persistent decline in kidney function was defined as an increase in serum creatinine of at least 50% from the pre-angiography baseline value to the measurement taken 90 days following angiography. The reported endpoint is a count of participants with an event, rather than a time-to-event estimate or a measurement of average kidney function. The record gives no separate primary-result counts for each component, so the composite result cannot establish which component contributed most to the total.

In general, a composite endpoint can capture several important outcomes in a single analysis and may increase the number of participants who meet the endpoint. Its interpretation depends on the components: a combined count does not mean that each component is equally frequent, equally serious, or affected in the same way. Here, the endpoint combines death, acute dialysis, and a defined kidney-function decline. The registry’s stated time window and definitions make clear what the reported primary count represents, but component-specific primary effects are not reported in the registry record.

7. Results Posted in the Registry

• Saline: 4.9% (116/2379) versus 4.6% (111/2393) on control; risk difference 0.2 percentage points (95% CI -1.0 to 1.4), risk ratio 1.05 (0.82–1.36); unadjusted two-proportion z-test p = 0.700.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry’s sponsor-reported analysis compares the two intravenous-fluid groups using an odds ratio and identifies Wald’s Chi-Square as the method. The endpoint is binary for each participant: the participant either met the composite event definition within the stated timeframe or did not. A count of participants with an event can therefore be compared between groups using measures of relative or absolute difference.

What does the risk difference express?

The recalculated risk difference is 0.002, with a confidence interval from -0.010 to 0.014. A risk difference subtracts one group’s event proportion from the other group’s event proportion. A value of zero corresponds to equal proportions. Its sign depends on the order in which the groups are compared, so the group order matters when interpreting direction. The recalculation uses the posted group counts and sizes and is unadjusted; it is not the sponsor’s reported effect measure.

What do relative measures add?

A risk ratio compares event proportions as a ratio, with 1 representing equal proportions. The recalculated risk ratio is 1.051, with a confidence interval from 0.815 to 1.355. An odds ratio compares event odds rather than event proportions. The recalculated odds ratio is 1.054, with a confidence interval from 0.807 to 1.376. The sponsor-reported odds ratio is 0.95, with a 95% confidence interval from 0.73 to 1.24. The values are on different scales or come from different analyses, so they should not be treated as interchangeable estimates. The registry does not identify a discrepancy.

In general, an odds ratio of 1 and a risk ratio of 1 represent no relative difference, while a risk difference of zero represents no absolute difference. A confidence interval gives a range of values compatible with the data and the method’s assumptions. When an interval includes its no-difference reference value, the data do not rule out that value at the corresponding confidence level. That does not establish exact equality. The posted intervals include their relevant reference values.

How does the sponsor’s test work?

Wald’s Chi-Square is a general large-sample method for testing whether an estimated effect differs from its null value, using the estimate in relation to its estimated uncertainty. In general, a test statistic that is large relative to its uncertainty is less compatible with the null hypothesis. The registry reports p = 0.70 for the sponsor’s comparison. A p-value describes how unusual results at least this incompatible with the null would be under the test’s assumptions if the null were true; it is not the probability that the null is true, nor the probability that the observed result occurred by chance in an unrestricted sense.

The sponsor’s analysis is identified as a superiority analysis. In general, a superiority test asks whether the data support a difference in a specified direction or contrast, according to the prespecified analysis. A failure to reject a no-difference hypothesis is not a demonstration of equivalence or noninferiority; those conclusions require a suitable design and criteria. The equivalence or noninferiority framework and margins are not reported in the registry record.

The recalculated measures are simple, unadjusted calculations from the posted summary statistics. They do not substitute for the sponsor’s own analysis, which is reported as an odds ratio using Wald’s Chi-Square. The recalculated p-value is 0.7, while the sponsor reports p = 0.70; these values express the same rounded result. Since the registry does not flag a discrepancy, the recalculations can be read as supplemental descriptions of the posted counts, not as a replacement analysis.

What can the factorial design tell us?

In general, a factorial trial assigns participants across combinations of treatment factors, allowing investigators to study each factor and potentially whether the factors interact. An interaction would mean that the effect associated with one factor varies depending on the assignment of the other factor. This trial has two factors, intravenous fluid and oral capsule. The posted primary result compares bicarbonate with saline, while the record does not report a result for the oral treatment contrast or an interaction analysis. It is therefore not possible to infer those effects from the intravenous-fluid comparison alone.

Statistical methods depend on the analysis population, data completeness, and model specifications. Those details—including covariate adjustment, the exact analysis population, and missing-data handling—are not reported in the registry record. The reported method and estimates should be interpreted within that limit rather than as a complete account of the trial’s analysis plan.

10. Confidence Intervals and Precision

The sponsor-reported odds ratio is 0.95, with a 95% confidence interval from 0.73 to 1.24. The interval includes 1, the no-difference value for an odds ratio. It is compatible with odds on either side of that reference, so the estimate does not precisely determine the direction of the effect. The point estimate alone should not be read without the interval.

The recalculated risk difference is 0.002, with a confidence interval from -0.010 to 0.014. A risk difference of zero represents equal event proportions. Since the interval extends on both sides of zero, the posted summary statistics are compatible with a range of absolute differences in either direction. The recalculated risk ratio is 1.051, with a confidence interval from 0.815 to 1.355, and the recalculated odds ratio is 1.054, with a confidence interval from 0.807 to 1.376. These intervals include 1, the no-difference reference for ratios.

In general, a confidence interval reflects both the observed estimate and its statistical uncertainty under the method used. A narrower interval indicates greater precision on that measure’s scale; a wider interval indicates more uncertainty about the effect’s magnitude. The interval is not a range guaranteed to contain the true effect, and it does not assign a probability to the true effect after the data are observed.

Here, the point estimates are close to their respective no-difference values, but the intervals leave room for effects in either direction. They do not establish that the groups are identical, and they do not identify a precise clinically important difference. The registry does not report a prespecified threshold for clinical importance, so statistical precision cannot be translated into a claim about whether a particular difference would matter clinically.

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 event counts. They illustrate the number of participants per arm that a hypothetical two-arm comparison would require under the stated assumptions. The calculations use 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 the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the specified effect under the calculation’s assumptions, if that effect is the true effect. The 90% power column gives the corresponding planning number for a 90% chance under those assumptions. Power is a property of a planned design relative to a specified effect and analysis; it is not a measure of whether the observed result is true.

The rows use planning for 100%, 75%, and 50% of the observed effect. For example, the row for 100% of the observed effect lists 126,127 participants per arm for 80% power and 168,848 participants per arm for 90% power. The rows for smaller fractions require more participants: the row for 75% lists 222,897 and 298,396 participants per arm, while the row for 50% lists 498,526 and 667,385 participants per arm, respectively. The curve should be read as the same relationship between assumed effect size and required sample size, rather than as observed trial outcomes.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect generally requires more participants. These figures are a planning illustration computed from the observed effect, not observed power and not evidence that the completed trial had those design characteristics.

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 = 0.046; treatment proportion p₁ = 0.049; average p̄ = 0.048.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3010 = 0.5900.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3010 = 0.2533.
4. n = (0.5900 + 0.2533)² / (0.0024)² = 126,126.9, rounded up to 126,127 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 <- 0.0463852904304221                          # control proportion
p1 <- 0.0487599831862127                          # 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(1467466)
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 = 126,127 (80% power), 168,848 (90% power)
 75% of observed effect: n per arm = 222,897 (80% power), 298,396 (90% power)
 50% of observed effect: n per arm = 498,526 (80% power), 667,385 (90% power)
power.prop.test: 126126.9 
Simulated power at n = 126,127 per arm: 0.801 (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. Analyses Reported by the Sponsor

The sponsor-reported result is an odds ratio of 0.95, with a 95% confidence interval from 0.73 to 1.24 and p = 0.70, using Wald’s Chi-Square. The recalculated results use the posted group counts and are unadjusted: the risk difference is 0.002, with a confidence interval from -0.010 to 0.014 and p = 0.7. The recalculation also gives a risk ratio of 1.051 and an odds ratio of 1.054, each with its reported confidence interval.

These analyses present the comparison on different scales and are not identical calculations. The sponsor’s estimate is the registry-reported analysis; the recalculated estimates provide additional descriptions derived from the posted summaries. The registry does not flag a discrepancy. Both the sponsor’s reported odds-ratio interval and the recalculated intervals include their respective no-difference values, and the p-values are reported as 0.70 and 0.7.

The recalculation cannot reproduce unreported details of the sponsor’s analysis, such as any model specifications or adjustments. It should therefore be treated as a simple check based on the available counts, not as a replacement for the sponsor’s analysis. The registry record does not report enough statistical-plan detail to explain any potential differences between methods beyond the measures and test it names.

14. Multiplicity, Missing Data and Analysis Populations

The primary outcome is a composite endpoint for the bicarbonate-versus-saline comparison. The record lists two outcome measures and two analyses, but no secondary outcomes are posted. It does not report the full list of planned hypotheses, whether additional analyses were prespecified, or how the testing of multiple outcomes or treatment contrasts was handled.

Multiplicity arises in general when several hypotheses are tested or several analyses are used to support conclusions. Repeated testing can increase the chance of a statistically notable finding even when no true effect exists. Methods such as a prespecified testing hierarchy or adjustment can address this concern, but the registry’s multiplicity plan is not reported in the registry record. It is therefore not possible to determine whether the reported p-value was adjusted, whether other planned tests were performed, or how the primary comparison fit into an overall testing strategy.

The trial is described as factorial, with intravenous-fluid and oral-capsule factors. The registry’s primary result reports the intravenous-fluid comparison, but a separate result for N-acetylcysteine versus placebo and an interaction analysis are not reported in the registry record. The intended statistical handling of those factors, including whether an interaction was considered in the primary analysis, is not reported either. The absence of a posted result should not be taken to mean that no such analysis was conducted.

The record does not report whether the analysis followed intention-to-treat, per-protocol, or another population definition. It does not describe missing outcome data, loss to follow-up, imputation, exclusions, or how the analysis handled participants without an available 90-day measurement. The precise analysis population and missing-data methods are therefore not reported in the registry record.

Interim analyses, stopping rules, covariate adjustments, and the original statistical analysis plan are also not reported in the registry record. These omissions limit the ability to evaluate the entire analysis process or determine how the posted comparison relates to every prespecified analysis. The reported estimate and its uncertainty can be interpreted as posted, while these unreported design and analysis details remain unresolved.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: coronary artery disease (14.6%), acute kidney injury (5.6%), cardiac failure congestive (4.7%), aortic valve stenosis (3.7%), atrial fibrillation (2.5%).

The registry lists adverse-event information separately for the four treatment combinations. For saline with oral placebo, 1300 were listed as at risk for serious events and 941 as affected; 1300 were listed as at risk for other events and 61 as affected, with 28 deaths. For saline with oral N-acetylcysteine, the corresponding figures are 1292, 1040, 1292, and 158, with 40 deaths. For bicarbonate with oral placebo, they are 1294, 1083, 1294, and 83, with 33 deaths. For bicarbonate with oral N-acetylcysteine, they are 1291, 941, 1291, and 170, with 28 deaths.

These are registry-listed counts by treatment combination; they should not be treated as the primary composite endpoint comparison. The adverse-event information does not specify in this record how these figures relate to event severity, causation, or the primary outcome’s definitions. The listed serious terms include coronary artery disease at 14.6%, acute kidney injury at 5.6%, cardiac failure congestive at 4.7%, aortic valve stenosis at 3.7%, atrial fibrillation at 2.5%, and acute myocardial infarction at 2.2%. These reported terms and percentages do not establish that a treatment caused an event or permit a causal comparison between groups.

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

The main result is a comparison of the number of participants who experienced the composite endpoint within 90 days after angiography. The registry reports 111 events among 2393 participants in the bicarbonate group and 116 among 2379 in the saline group. The sponsor’s odds ratio is 0.95, with a 95% confidence interval from 0.73 to 1.24 and p = 0.70. The unadjusted recalculation gives a risk difference of 0.002, with a confidence interval from -0.010 to 0.014. These results do not show a statistically clear difference between the intravenous-fluid groups.

That interpretation is not the same as concluding that the treatments have identical effects. The confidence intervals include no difference but also allow values on either side of it. The record does not report an equivalence margin or a noninferiority design, so the absence of a statistically clear difference cannot be used to claim equivalence or noninferiority.

The endpoint combines death, acute dialysis, and a persistent decline in kidney function defined using serum creatinine. The registry does not post separate primary results for those components. Accordingly, the overall result cannot determine whether any one component drove the composite or whether the components had different patterns.

The trial purpose names both intravenous-fluid and oral-capsule comparisons, but the posted primary result concerns bicarbonate versus saline. The N-acetylcysteine-versus-placebo result and any interaction between the treatment factors are not reported in the registry record. The primary comparison therefore does not answer every treatment question raised by the factorial design.

Finally, the reported results should be read in light of details that are absent from the record, including the exact analysis population, missing-data handling, adjustment strategy, and full multiplicity plan. The statistics describe the posted comparison and its uncertainty. They do not establish cause beyond the randomized comparison, predict an individual participant’s outcome, or provide medical advice.

17. Why This Trial Matters Statistically

This trial illustrates why an effect estimate should be read together with its uncertainty. The primary event counts are close, and the sponsor-reported odds ratio is near its no-difference reference. Yet the confidence interval, rather than the point estimate alone, shows that the registry results remain compatible with effects in either direction. Statistical interpretation depends on both what was estimated and how precisely it was estimated.

The endpoint also demonstrates a challenge of composite outcomes. Combining death, acute dialysis, and persistent kidney-function decline gives a single primary count, but the components differ in meaning. Without component-specific primary results, the overall estimate cannot reveal whether the components behaved similarly. This distinction matters when interpreting what a composite result can and cannot describe.

The factorial design provides a useful example of the difference between a study’s treatment structure and its posted results. The trial included two treatment factors and four combinations, while the primary reported estimate compares the intravenous-fluid groups. The posted primary comparison does not supply a result for the oral treatment contrast or an interaction analysis. A design may raise several statistical questions even when only some results are available in the registry record.

Finally, the unadjusted recalculations and sponsor-reported odds ratio demonstrate that estimates can be expressed on different scales. Absolute and relative measures answer related but distinct questions. Their intervals help communicate uncertainty, while the registry’s limited reporting of analysis details constrains how far the results can be evaluated. Together, these features show why clear separation of design, endpoint, effect measure, precision, and unreported analysis details is important in reading trial results.

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.

The registry record does not provide the full eligibility criteria or a detailed description of the high-risk population. Although acute renal failure, kidney disease, and coronary artery disease are listed as conditions, those entries do not establish that every participant had each condition. The results should be understood as applying to the trial groups described in the record, rather than to a more specific subgroup definition that is not reported.

The primary result is for a composite endpoint, and separate primary estimates for death, acute dialysis, and persistent kidney-function decline are not reported in the registry record. The study’s purpose includes the oral N-acetylcysteine-versus-placebo comparison, but that outcome contrast is not posted. An interaction result for the two treatment factors is also not reported. These gaps limit interpretation of the full factorial question and the components of the composite.

The record does not report the original sample-size justification, the detailed statistical analysis plan, analysis populations, missing-data methods, interim analyses, stopping rules, or multiplicity approach. It is consequently not possible to assess those aspects of the conduct and analysis from the registry information. The planning illustration based on fractions of the observed effect should not be confused with the trial’s original design calculation.

The posted adverse-event counts are given for the four treatment combinations, but the record does not explain how to interpret their relationship to the primary endpoint or establish causation. The adverse-event figures therefore cannot replace the primary comparison or support causal conclusions about individual listed events. These reporting limitations do not alter the estimates that are posted, but they bound what can be concluded from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prevention of Serious Adverse Events Following Angiography — NCT01467466.
• Registry record last updated 2025-11-05; status last verified 2025-10.
• Results first posted 2018-11-09.
• 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

The registry describes NCT01467466, “Prevention of Serious Adverse Events Following Angiography,” also titled CSP #578 - Prevention of Serious Adverse Events Following Angiography (PRESERVE). It is listed as a completed Phase 3, randomized, double-masked factorial trial sponsored by the VA Office of Research and Development, with enrollment of 5177.

The four treatment combinations paired intravenous saline or bicarbonate with oral placebo or N-acetylcysteine. The primary outcome counted participants with death, need for acute dialysis, or persistent kidney-function decline within 90 days following angiography. The posted primary comparison reports 111 events among 2393 participants assigned bicarbonate and 116 among 2379 assigned saline. The sponsor-reported odds ratio is 0.95, with a 95% confidence interval from 0.73 to 1.24 and p = 0.70.

The posted result does not establish a statistically clear difference between the intravenous-fluid groups. Results for the oral treatment contrast, component-specific primary outcomes, and several analysis-plan details are not reported in the registry record.