Efficacy and Safety of FP-1201-lyo (Interferon Beta-1a) in Prevention of Multi-Organ Failure on Patients After Open Surgery for a RAAA: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of FP-1201-lyo (Interferon Beta-1a) in Prevention of Multi-Organ Failure on Patients After Open Surgery for a RAAA (NCT03119701), a randomized phase 2 study. The primary outcome is The Efficacy of FP-1201-lyo Compared to Placebo Concerning All Cause Mortality.

2. Clinical Question

The trial asked whether FP-1201-lyo (interferon beta-1a), compared with placebo, affected all-cause mortality by Day 30 in patients who survived open surgery for a ruptured abdominal aortic aneurysm. The primary outcome counted participants who died. The primary analysis population was the Full Analysis Set for Efficacy: randomized patients who received study treatment, excluding those who died within 36 hours of their first dose.

The registry describes a randomized, parallel-group comparison with a 2:1 allocation in its official title. The posted primary results report 6 fatalities among 27 participants in the FP-1201-lyo group and 2 among 11 in the placebo group. These counts describe the recorded outcome; they do not by themselves establish a treatment effect. The analysis and its uncertainty need to be considered alongside the population definition and the small number of outcome events.

3. Trial Design

The registry identifies NCT03119701 as a phase 2, randomized, parallel-group trial comparing FP-1201-lyo 10 µg with placebo. Its official title describes a 2:1 comparison, and masking is listed as quadruple. The recorded enrollment is 40. The trial status is terminated; the reason for termination is not reported in the registry record.

The treatment descriptions specify daily intravenous bolus injections for 6 days in both groups. The FP-1201-lyo formulation was described as a lyophilisate reconstituted in water for injection, and the placebo description gives the same formulation and administration route. The clinical setting was prevention of multi-organ failure after open surgery for a ruptured abdominal aortic aneurysm.

The primary endpoint was a participant count for all-cause mortality at Day 30. The primary analysis population was not simply all randomized patients: it included randomized patients who received study treatment, while excluding deaths within 36 hours from the first dose. The registry’s posted arm counts for this endpoint are 27 in the FP-1201-lyo group and 11 in the placebo group. The record does not explain how these endpoint counts relate to the recorded enrollment, nor does it report a detailed account of participant flow.

The registry also lists mortality at Day 90 and outcomes concerning ventilator-free days, hemodialysis, organ-failure-free days assessed with the SOFA score, abdominal compartment syndrome, neutralizing antibodies, disability, and safety. The trial’s original sample-size assumptions, detailed allocation procedures, and reasons for termination are not reported in the registry record. The record identifies logistic regression for the sponsor’s primary analysis, but a fuller statistical analysis plan is not reported.

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.

6-day Dosing

Reasons for not completing this period:

Mid-term (Final) Follow-up at D90

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set for Efficacy (FAS-E) defined as all randomised patients who received study treatment, excluding the early deaths (within 36 hours from first dose of the study treatment).

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 40 subjects received at least 1 dose of study drug. 2 patients were excluded from Full Analysis Set for Efficacy (FAS-E) and Per Protocol Set (PPS) populations due to early deaths (within 36 hours from first dose of the study treatment). Therefore, FAS-E and PPS populations consisted of 38 patients.

6. Primary Endpoint

The registry lists the primary outcome as The Efficacy of FP-1201-lyo Compared to Placebo Concerning All Cause Mortality, measured over Day 30.

The primary endpoint counts fatalities from any cause by Day 30. It is a binary participant-level outcome: each person in the analysis population is classified according to whether a death was recorded within the stated timeframe. The registry describes the endpoint unit as participants and the outcome as the number of fatalities.

Mortality is a direct, clinically important outcome in a study of patients after emergency open surgery for a ruptured abdominal aortic aneurysm. A fixed assessment timeframe makes the outcome interpretable as the proportion of the defined population with a recorded death by that point. Here, however, the population definition matters: the primary efficacy set excludes patients who died within 36 hours of the first study-treatment dose and excludes randomized patients who did not receive treatment. The resulting estimate therefore addresses the specified treated efficacy population, not every person initially considered for the trial.

The posted counts are 6 fatalities among 27 participants receiving FP-1201-lyo and 2 among 11 receiving placebo. Counts alone do not account for the different group sizes or quantify the uncertainty in a between-group comparison. The registry also gives a logistic-regression analysis of the odds ratio. Neither a numerical estimate nor a significance test can, on its own, settle whether the groups differed in a way that is clinically meaningful. Interpretation must account for the wide uncertainty and the limited number of observed events.

7. Results Posted in the Registry

• FP-1201-lyo 10 µg: 22.2% (6/27) versus 18.2% (2/11) on control; risk difference 4.0 percentage points (95% CI -23.6 to 31.7), risk ratio 1.22 (0.29–5.15); unadjusted two-proportion z-test p = 0.782.

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.

The Efficacy of FP-1201-lyo Compared to Placebo Concerning All Cause Mortality

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • FP-1201-lyo 10 µg: 25.9% (7/27) versus 18.2% (2/11) on control; risk difference 7.7 percentage points (95% CI -20.4 to 35.9), risk ratio 1.43 (0.35–5.82); unadjusted two-proportion z-test p = 0.611.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FP-1201-lyo 10 µg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering mortality, ventilator-free days, days receiving hemodialysis, organ-failure-free days assessed by SOFA, abdominal compartment syndrome, neutralizing antibodies, disability measured with the modified ranking scale, and safety. These outcomes span survival, organ support, organ dysfunction, a physiological complication, immune response, disability, and adverse events. They provide context for the wider set of questions considered in the trial, but they are not interchangeable with the primary Day 30 mortality endpoint.

The registry also contains a Day 90 mortality comparison. Its reported estimate is imprecise, as is the primary mortality comparison. The available information does not support describing a consistent pattern across all secondary outcomes: numerical results and analysis details for the other listed outcomes are not reported in the registry record. Their direction, magnitude, and precision therefore cannot be characterized from the information available.

Secondary outcomes can help describe different aspects of a trial, but they generally carry less confirmatory weight than a designated primary outcome. Testing many outcomes creates more opportunities for chance findings. Unless a statistical plan prespecifies how multiplicity will be handled, an apparently notable result among secondary endpoints needs cautious interpretation. The registry record does not report a multiplicity-adjustment strategy, so the secondary outcomes should be treated as exploratory or supportive rather than as independent confirmation of the primary result.

Differences in outcome type and measurement also matter. A participant count for mortality is not measured on the same scale as days free of ventilation, a SOFA-based outcome, or a disability score. The interpretation of each requires its own endpoint definition and analysis details, which are not fully reported for the secondary outcomes in the registry record.

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

• The Efficacy of FP-1201-lyo Compared to Placebo Concerning All Cause Mortality
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Number of Ventilator Free Days (VFDs)
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Number of Days Receiving Hemodialysis
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Number of Organ Failure Free Days by Means of the Sequential Organ Failure Assessment (SOFA) Score
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Prevalence of Abdominal Compartment Syndrome by Intra-abdominal Pressure (IAP)
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Neutralizing Antibodies Against IFN Beta-1a (NAbs) in Whole Blood Samples
• The Efficacy of FP-1201-lyo Compared to Placebo Concerning Disability by Modified Ranking Scale (mRS).
• Safety Parameters of Clinically Significant Treatment Emergent Adverse Events (TEAEs), Serious Adverse Events, Vital Signs and Clinical Laboratory Parameters

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports logistic regression for the sponsor’s primary comparison and presents the result as an odds ratio. An unadjusted recalculation from the posted summary counts is also available. These methods answer related but not identical questions, so it is useful to distinguish the reported model-based estimate from a simple comparison of the observed group summaries.

What does an odds ratio describe?

An odds ratio compares the odds of an event in one group with the odds in another. An odds ratio of 1 represents equal odds. Values above 1 indicate higher estimated odds in the group named first in the comparison; values below 1 indicate lower estimated odds. Odds are not the same quantity as risk, especially when events are not rare. The odds ratio is also not a direct count of how many additional or fewer participants experienced an event.

For the primary endpoint, the sponsor’s logistic-regression odds ratio is 1.30. The registry record does not report enough detail to establish whether the model included covariates or other adjustments, so it is best described as the sponsor’s reported logistic-regression analysis rather than characterized as adjusted or unadjusted. The exact model specification is not reported in the registry record.

What does the unadjusted recalculation add?

The recalculation uses the posted group counts to estimate a simple, unadjusted contrast. It does not reproduce undocumented model choices or account for participant-level information. It is useful as a check on the direction and broad scale of the reported result, but the sponsor’s analysis is the registry’s own reported analysis. In this trial, the record does not flag a discrepancy, and the recalculation and sponsor analysis lead to a similar broad reading: the estimate is uncertain and does not show a clear difference.

A risk difference expresses the difference between group risks on an absolute scale. A confidence interval for a risk difference that includes zero is compatible with no absolute difference as well as with effects in either direction. The primary recalculation’s interval spans zero. This describes statistical uncertainty, not proof that the risks are identical.

How should the p-value be read?

A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The sponsor’s primary p-value is 0.78, while the unadjusted recalculation gives 0.782. These values do not indicate strong evidence against the null in the corresponding analyses. They do not establish equivalence or rule out meaningful differences.

General statistical context: when event counts are limited, estimates can vary substantially with the observed outcomes, and confidence intervals can be wide. A non-significant result in a small trial may reflect limited information rather than evidence that the groups are identical. For that reason, the estimated effect and its interval are important companions to a p-value.

Why do confidence intervals matter?

A confidence interval gives a range of effect estimates compatible with the data under the statistical method and its assumptions. It communicates precision: narrower intervals indicate more precise estimates, while wider intervals indicate less precision. It is not a guarantee that the true effect lies inside the particular interval. For the sponsor’s primary odds ratio, the reported interval extends from below 1 to well above 1, leaving substantial uncertainty about the direction and size of the underlying association.

What are the limits of the registry analysis?

The record identifies the primary efficacy population and the endpoint, but it does not report a full statistical analysis plan, model specification, missing-data procedures, interim-analysis arrangements, or the original sample-size justification. These details should not be inferred from the reported method alone. The posted efficacy population also excludes early deaths within 36 hours of the first dose, a definition that shapes the question answered by the primary analysis.

General statistical context: analyses of several outcomes raise multiplicity concerns because repeated testing increases the opportunity for apparently notable findings by chance. The registry lists a range of secondary outcomes, but a multiplicity-adjustment approach is not reported in the registry record. Secondary findings should therefore be interpreted cautiously, particularly when they are not supported by a prespecified analysis plan or a clearly reported adjustment strategy.

11. Confidence Intervals and Precision

The sponsor’s primary odds-ratio estimate is 1.30, with a 95% confidence interval from 0.21 to 8.19. The interval includes 1, the value representing equal odds, and extends across a broad range on both sides. This means the estimate is not precise enough to pin down the direction or size of the association. The sponsor reports p = 0.78, consistent with the interval’s lack of clear evidence against equal odds under that analysis.

The unadjusted recalculation of the primary risk difference also has an interval that includes zero. Zero represents no absolute difference between the group risks. Thus, the recalculation does not tightly distinguish an increase from a decrease, and it should not be read as showing that the risks are the same. Its p-value is 0.782.

These wide intervals are important in a trial with few observed fatalities. A point estimate gives one central summary, but it cannot capture the range of effect sizes compatible with the data. The Day 30 counts—6 of 27 in the FP-1201-lyo group and 2 of 11 in the placebo group—provide limited information for estimating a between-group effect. General statistical context: fewer observed events usually mean less information for estimating a binary-outcome contrast, particularly when groups are small.

The Day 90 sponsor interval, from 0.28 to 10.52 for the odds ratio, is also broad and includes 1. Taken together, the mortality estimates are too imprecise to support a confident claim about the direction or magnitude of a treatment effect. Confidence intervals express uncertainty under the chosen method; they do not account for every possible source of bias, missing information, or limitations in the trial design.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For this binary mortality endpoint, the figures are participants per arm, not total events. The registry record’s sample-size assumptions for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The scenarios plan for detecting 100%, 75%, or 50% of the observed effect.

The 80% power column indicates the illustrative number of participants per arm under those assumptions for an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning figure for a 90% chance. These are prospective planning concepts, not descriptions of what happened in this trial.

The figures change with the assumed fraction of the observed effect. Planning for a smaller effect requires more participants because smaller differences are harder to distinguish from random variation. The values are not recommendations for a future study: appropriate planning also depends on the intended target effect, outcome definition, allocation, analysis, and other design choices.

The registry record does not report the trial’s own original sample-size assumptions or justification. The displayed planning figures are not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after results are known; the interval is the more direct guide to how much uncertainty remains in these data.

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 = 0.182; treatment proportion p₁ = 0.222; average p̄ = 0.202.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5678 = 1.1129.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5671 = 0.4773.
4. n = (1.1129 + 0.4773)² / (0.0404)² = 1,549.0, rounded up to 1,549 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 <- 0.181818181818182                          # control proportion
p1 <- 0.222222222222222                          # 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(3119701)
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 = 1,549 (80% power), 2,074 (90% power)
 75% of observed effect: n per arm = 2,703 (80% power), 3,618 (90% power)
 50% of observed effect: n per arm = 5,964 (80% power), 7,984 (90% power)
power.prop.test: 1549 
Simulated power at n = 1,549 per arm: 0.806 (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

For Day 30 mortality, the sponsor reports a logistic-regression odds ratio of 1.30, with a 95% confidence interval from 0.21 to 8.19 and p = 0.78. The unadjusted recalculation from the posted summaries gives an odds ratio of 1.286 and p = 0.782. The registry record does not flag a discrepancy between these analyses, and their broad interpretation is similar: the estimate is imprecise and does not show a clear difference between groups.

The sponsor’s result is the trial’s reported analysis. The recalculation is a simple unadjusted check from summary statistics; it does not reproduce details of the sponsor’s regression model. The registry does not report enough model specification to explain any small numerical differences. Since the record identifies no discrepancy, there is no indication that the recalculation conflicts materially with the sponsor’s reported conclusion.

For Day 90 mortality, the sponsor reports an odds ratio of 1.7, a 95% confidence interval from 0.28 to 10.52, and p = 0.57. The unadjusted recalculation gives p = 0.611. This secondary comparison is also imprecise. The two analyses should be understood in their respective roles: the sponsor analysis is the reported trial analysis, while the recalculation is a transparent check based on posted summary counts.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary mortality endpoint and lists multiple secondary outcomes. It does not report whether the secondary tests were adjusted for multiplicity, whether a hierarchy among secondary outcomes was prespecified, or whether any outcomes were designated as confirmatory. Without those details, the chance of obtaining a seemingly notable result from repeated testing cannot be assessed from the registry record.

Multiplicity is a general statistical concern when several hypotheses are tested. If each is assessed without accounting for the others, the probability of at least one chance finding can increase. Adjustment methods or a prespecified testing order can address this concern, but the appropriate approach depends on the aims and design. No particular approach should be assumed for this trial because one is not reported in the registry record.

The primary analysis population is defined as randomized patients who received study treatment, excluding deaths within 36 hours of the first dose. This is important for interpretation: it differs from an analysis of every randomized patient and omits a group defined by an early post-dose event. The registry does not report a separate estimate including those early deaths, nor does it explain the rationale for excluding them. The record also does not provide a detailed participant-flow account that would clarify all differences between enrollment and endpoint analysis counts.

Methods for handling missing outcome data, withdrawals, or other incomplete observations are not reported in the registry record. Nor are sensitivity analyses described that would show how alternative missing-data assumptions might affect the results. The original sample-size justification, interim-analysis plans, and a full statistical analysis plan are likewise not reported. These omissions limit assessment of whether the reported analysis followed a prespecified plan and how robust the findings are to analytic choices.

These gaps do not change the reported estimates, but they narrow what can be concluded from them. The broad confidence intervals, limited event counts, selected analysis population, and unreported multiplicity and missing-data procedures all warrant restrained interpretation.

16. 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: multiple organ dysfunction syndrome (13.8%), intestinal ischaemia (10.3%), large intestine perforation (10.3%), pneumonia (9.1%), pulmonary contusion (9.1%).

The registry reports serious adverse events for 13 of 29 participants at risk in the FP-1201-lyo group and 3 of 11 at risk in the placebo group. It reports other adverse events affecting 27 of 29 at risk in the FP-1201-lyo group and 9 of 11 in the placebo group. Deaths are recorded separately as 7 and 2, respectively. These safety denominators differ from the primary efficacy analysis counts; the registry record does not explain the differences in detail.

The most frequently listed serious-event terms include multiple organ dysfunction syndrome (13.8%), intestinal ischaemia (10.3%), large intestine perforation (10.3%), pneumonia (9.1%), pulmonary contusion (9.1%), and road traffic accident (9.1%). The percentages are registry entries and should not be interpreted as proving that treatment caused these events. Patients in this setting may experience serious complications, and the information reported does not establish attribution for individual events.

Safety counts describe events observed and recorded in each group; they do not, by themselves, establish comparative safety. The record does not provide enough detail to determine event timing, severity grading, relatedness assessments, or the statistical approach to comparing safety outcomes. Because this was a small trial, the safety data have limited ability to characterize uncommon harms.

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

The results describe a randomized phase 2 comparison of FP-1201-lyo and placebo in patients after open surgery for a ruptured abdominal aortic aneurysm. For the primary Day 30 mortality endpoint, the registry records 6 fatalities among 27 participants in the FP-1201-lyo group and 2 among 11 in the placebo group. The sponsor’s odds-ratio estimate is 1.30, with a wide 95% confidence interval from 0.21 to 8.19 and p = 0.78.

These data do not provide a precise estimate of the difference between groups. The interval includes equal odds and allows a wide range of possible associations. The non-significant result is not proof of no effect, and it does not demonstrate that the treatments are equivalent. Conversely, the point estimate alone does not establish that FP-1201-lyo increases mortality or causes harm. The trial’s results should be described as uncertain rather than as a definitive finding in either direction.

The findings also do not answer every question about multi-organ failure. Mortality is the primary endpoint, while the registry lists other outcomes related to organ support and dysfunction. Numerical results and sufficient analysis detail for those other outcomes are not reported in the registry record available for this analysis. No conclusion about their pattern should be inferred from the mortality result alone.

The population definition further limits the scope of the primary result: early deaths within 36 hours of the first dose were excluded from the efficacy set, as were randomized patients who did not receive study treatment. The result therefore pertains to the defined analysis population and should not be generalized automatically to all patients undergoing this surgery or to other treatment settings.

The record is marked terminated, but the reason is not reported in the registry record. Termination status alone does not explain why the trial ended and should not be treated as evidence about efficacy or safety. Overall, the posted data support a cautious description of an imprecise comparison, not a claim that treatment works, fails, or has a particular causal effect.

18. Why This Trial Matters Statistically

This trial illustrates several statistical issues that often arise in studies of rare, severe clinical outcomes. Mortality is a direct endpoint, but a small number of events can leave the estimated comparison highly uncertain. The point estimate and p-value are not enough: the width of the confidence interval shows that the data do not tightly determine either the direction or magnitude of an association.

The analysis population also matters. The registry’s primary efficacy set excludes early deaths within 36 hours of the first dose and includes only randomized patients who received treatment. That definition changes the population to which the primary estimate applies. Clear reporting of the population, participant flow, and the reasons for exclusions is essential to judge what question the analysis answers.

The study also has a broad set of secondary outcomes. Such outcomes can be valuable for describing survival, organ support, organ dysfunction, safety, and other domains, but they increase the importance of prespecifying hypotheses and handling multiplicity. The registry record does not report a multiplicity strategy or a full analysis plan, so secondary results need restrained interpretation.

Finally, the registry’s terminated status and the absence of reported original sample-size assumptions highlight the value of transparent trial records. The reason for termination and the trial’s own design justification are not reported. These limitations do not erase the results, but they shape how confidently they can be used. The central statistical lesson is that a randomized comparison can still yield an uncertain estimate when event information is limited and important analysis details are unavailable.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary efficacy population excludes deaths within 36 hours from the first study-treatment dose and excludes randomized patients who did not receive treatment. This selected population may not represent every randomized patient or all patients undergoing the surgery. The registry record does not explain the rationale for excluding early deaths or provide a parallel primary estimate using a broader population.

The posted primary comparison is based on a limited number of fatalities, and its confidence interval is wide. This limits precision and makes the estimate sensitive to the observed event pattern. The registry’s recorded enrollment and primary analysis counts are not the same; participant flow and the relationship between those figures are not explained in detail in the registry record.

The trial is marked terminated, but the reason for termination is not reported in the registry record. The original sample-size justification, full statistical analysis plan, interim-analysis arrangements, allocation procedures, and detailed logistic-regression specification are also not reported. Missing-data methods and sensitivity analyses are not described. These omissions prevent a full assessment of prespecification and robustness.

The registry lists a range of secondary endpoints, but complete numerical results and analysis details for those outcomes are not available in the information used for this account. A multiplicity strategy is not reported. Safety counts are recorded, but event attribution, timing, and detailed comparative methods are not available. The small trial and limited number of events also restrict what can be learned about uncommon safety outcomes.

These limitations do not imply that the reported results are invalid. They mean that the estimates need to be read within their defined population and with attention to their uncertainty, and that conclusions beyond the outcomes and analyses reported would be unsupported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of FP-1201-lyo (Interferon Beta-1a) in Prevention of Multi-Organ Failure on Patients After Open Surgery for a RAAA — NCT03119701.
• Registry record last updated 2021-01-14; status last verified 2020-12.
• Results first posted 2021-01-14.
• 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

NCT03119701 is a phase 2 randomized, quadruple-masked, parallel-group comparison of FP-1201-lyo 10 µg and placebo after open surgery for a ruptured abdominal aortic aneurysm. The official title describes a 2:1 comparison. The recorded enrollment is 40, and the registry status is terminated; the reason is not reported in the registry record.

The primary endpoint is all-cause mortality by Day 30 in a treated efficacy population that excludes early deaths within 36 hours of the first dose. The registry records 6 fatalities among 27 participants in the FP-1201-lyo group and 2 among 11 in the placebo group. The sponsor’s logistic-regression analysis reports an odds ratio of 1.30, a 95% confidence interval from 0.21 to 8.19, and p = 0.78. The estimate is imprecise and does not establish a clear difference between groups.

The registry lists additional efficacy and safety outcomes, but the original sample-size rationale, full analysis plan, multiplicity approach, missing-data methods, and reason for termination are not reported in the registry record.