SANICS II Trial: Stimulation of the Autonomic Nervous System in Colorectal Surgery by Perioperative Nutrition: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SANICS II Trial: Stimulation of the Autonomic Nervous System in Colorectal Surgery by Perioperative Nutrition (NCT02175979), a randomized na study. The primary outcome is Number of Patients Developing Postoperative Ileus.

2. Clinical Question

This is a comparison of participant counts for a binary outcome: each participant either met the registry’s ileus definition or did not. The central statistical issue is not only which arm had the larger posted count, but also how uncertain the estimated between-arm difference is. The registry reports an unadjusted comparison, and the interval around that estimate spans effects in either direction. The trial therefore addresses a clinically focused question, while the posted estimate should be read as uncertain rather than as a definitive demonstration of a difference.

3. Trial Design

SANICS II is listed as a completed, multicenter, prospective, randomized controlled trial with a parallel-group design. The registry describes masking as quadruple. It records an enrollment of 280 and reports outcome data for a standard arm with 133 participants and an enriched enteral nutrition arm with 132 participants. Reasons for any difference between the enrollment figure and outcome denominators are not reported in the registry record.

The intervention was enriched enteral tube feeding at 1.5ml/ minute perioperative. The comparator was standard care, described in the trial summary as fasting perioperatively. The record identifies Misha D.P. Luyer as sponsor. The recorded start is 2014-08, and primary completion is listed as 2017-03-20. The study phase is recorded as NA.

The primary outcome was the number of patients developing postoperative ileus, with an outcome timeframe of up to 3 weeks after surgery. Its stated definition focuses on absence of flatus or stool passage and inability to tolerate a regular oral diet between surgery and postoperative day 4. The registry also lists secondary outcomes involving anastomotic leakage, aspiration pneumonia, gastric motility, functional recovery, C-reactive protein, additional interventions, ICU admission, and health-related quality of life. Posted numerical results are available for the primary outcome and some secondary outcomes; the registry record does not provide posted analyses for every listed outcome.

Randomization and masking are important design features, but the registry record does not report the randomization procedure, how allocation was concealed, which groups of people were masked, or how masking was maintained. Protocol details beyond the registry descriptions are not reported in the registry record. Those omissions limit how much can be assessed about trial conduct from the record 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.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: in both arms, 140 patients participated. in the standard arm 7 patients had to quit the study because exclusion criteria were met, in the enriched enteral nutrition 8 patients had to quit the study because exclusion criteria were met, which is stated in the results participant flow.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients Developing Postoperative Ileus, measured over up to 3 weeks after surgery.

The primary endpoint counts participants who developed postoperative ileus. The registry’s description requires absence of flatus or stool passage and inability to tolerate a regular oral diet between surgery and postoperative day 4. The listed timeframe for the outcome is up to 3 weeks after surgery. This distinction matters: the definition describes the criteria used to identify ileus, while the timeframe states the period over which the outcome was assessed.

A participant count is a binary outcome summarized for each arm. It can be compared between groups using a risk difference, which expresses the difference between the proportions experiencing the event. The posted risk difference is 0.062 for enriched enteral nutrition relative to standard care. Its interval ranges from -0.042 to 0.166, so the estimate is compatible with effects on either side of no difference. The unadjusted p-value is 0.241.

This endpoint is used because postoperative ileus is one of the trial’s stated clinical concerns and the trial’s main objective includes investigating its relationship to perioperative nutrition. A clearly defined event helps make the comparison interpretable, though the registry record does not report additional adjudication details or information about how the endpoint was assessed. The counts describe the outcome as recorded; they do not, by themselves, establish why an event occurred or whether the intervention caused a difference.

7. Results Posted in the Registry

• Enriched Enteral Nutrition: 28.0% (37/132) versus 21.8% (29/133) on control; risk difference 6.2 percentage points (95% CI -4.2 to 16.6), risk ratio 1.29 (0.84–1.96); unadjusted two-proportion z-test p = 0.241.

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.

Anastomotic Leakage

• 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:
  • Enriched Enteral Nutrition: 9.1% (12/132) versus 8.3% (11/133) on control; risk difference 0.8 percentage points (95% CI -6.0 to 7.6), risk ratio 1.10 (0.50–2.40); unadjusted two-proportion z-test p = 0.813.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enriched Enteral Nutrition and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Needing Additional Surgical, Radiological or Endoscopic Interventions

• 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:
  • Enriched Enteral Nutrition: 11.4% (15/132) versus 15.8% (21/133) on control; risk difference -4.4 percentage points (95% CI -12.7 to 3.8), risk ratio 0.72 (0.39–1.33); unadjusted two-proportion z-test p = 0.293.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enriched Enteral Nutrition and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Needing ICU Admission

• 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:
  • Enriched Enteral Nutrition: 23.5% (31/132) versus 27.8% (37/133) on control; risk difference -4.3 percentage points (95% CI -14.8 to 6.2), risk ratio 0.84 (0.56–1.27); unadjusted two-proportion z-test p = 0.419.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enriched Enteral Nutrition and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several different aspects of postoperative recovery and complications, including anastomotic leakage, additional procedures, ICU admission, aspiration pneumonia, gastric motility, functional recovery, C-reactive protein, and health-related quality of life. The record lists these outcomes, but numerical results are posted for only some of them. The available estimates do not point uniformly in one direction, and their uncertainty is substantial. The posted comparisons should therefore be read as a partial and exploratory picture rather than as a consistent pattern across every listed outcome.

These outcomes complement the primary ileus endpoint by addressing related complications, care needs, and recovery measures. They can help describe the broader clinical questions the trial sought to examine, but they do not substitute for the primary outcome. Nor do secondary comparisons establish or overturn the primary result: each outcome measures a different event or construct, and its estimate has its own uncertainty.

Unadjusted secondary results carry less weight because several outcomes create multiple opportunities for apparently noteworthy findings to arise by chance. The registry record does not report a multiplicity correction, a hierarchy of secondary endpoints, or whether the posted secondary analyses were intended to be confirmatory. Without those details, a nominal result on one outcome should not be treated as conclusive evidence. The absence of a posted analysis for other listed outcomes also means that the record does not allow a complete assessment of the whole secondary-outcome set.

Viewed alongside the primary result, the secondary information does not resolve the uncertainty about postoperative ileus. It provides additional outcome-specific comparisons, but the registry record does not report enough about analysis planning, missing data, or endpoint methods to support stronger claims across the range of outcomes.

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

• Anastomotic Leakage
• Aspiration Pneumonia
• Gastric Motility
• Functional Recovery
• C-reactive Protein (CRP)
• Number of Patients Needing Additional Surgical, Radiological or Endoscopic Interventions
• Number of Patients Needing ICU Admission
• Health-related Quality of Life

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is a comparison of a binary outcome: each participant is classified according to whether postoperative ileus was recorded. The arm-level summaries are event counts and participant denominators. For this kind of outcome, an event proportion describes the share of participants in an arm with the event, while a risk difference compares the two arm proportions by subtraction. The posted risk difference is 0.062, calculated with enriched enteral nutrition relative to standard care. Positive values correspond to a higher event proportion in the intervention arm; negative values correspond to a lower one.

What does the confidence interval tell us?

A confidence interval describes uncertainty around an estimated effect under the statistical method used. It is not a range containing a known fixed share of individual outcomes, and it does not assign a probability to the treatment effect being inside the particular interval. Instead, it indicates which effect values are reasonably compatible with the observed data and the method’s assumptions. The primary interval extends from -0.042 to 0.166. Because it spans negative and positive values, it does not resolve the direction of the difference. Its breadth also signals that the point estimate should not be treated as exact.

How should the p-value be read?

The primary unadjusted p-value is 0.241. A p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. A p-value above a conventional threshold does not prove equivalence or show that no meaningful effect exists. The registry record does not report the trial’s prespecified statistical analysis plan or the exact testing procedure, so the posted p-value should be interpreted as the unadjusted comparison reported in the outcome summary.

Why consider more than one effect measure?

The registry also posts relative measures for the primary comparison: a risk ratio of 1.286, with interval limits of 0.843 and 1.961, and an odds ratio of 1.397, with interval limits of 0.798 and 2.445. A risk ratio compares event proportions as a ratio; an odds ratio compares event odds. These measures express the same group comparison on different scales and should not be confused with the risk difference. Each posted interval spans values consistent with effects in either direction relative to no difference on its scale. Relative measures can look larger or smaller than an absolute difference depending on the event frequency, so interpretation should consider the measure’s scale and the observed event counts.

Why can secondary comparisons be harder to interpret?

When several outcomes are examined, some comparisons may look unusual by chance alone, even if no underlying differences exist. This is the general statistical issue of multiplicity. The registry lists multiple secondary outcomes, but it does not report a multiplicity adjustment or a prespecified hierarchy for interpreting them. The posted secondary p-values are therefore unadjusted and should not be treated as if they were the sole test in the trial. The record does not report whether the secondary outcomes were intended as confirmatory or exploratory.

Counts also depend on the outcome definitions and the availability of measurements. Missing outcome data can affect the validity of an estimate if the probability of missingness differs between arms or is related to outcome status. The registry record does not report missing-data counts, handling methods, or analysis populations for the primary or secondary outcomes. It also does not state whether every randomized participant was analyzed in the assigned group. Those details are important when assessing whether the observed comparison preserves the benefits of randomization.

Finally, the registry’s planning illustrations are separate from the trial’s original design calculations. They use an observed effect and stated planning assumptions to illustrate possible future sample sizes. They do not replace the sponsor’s analysis and are not a measure of the probability that this completed trial detected an effect. General statistical concepts can clarify how to read the summaries, but unreported design and analysis choices cannot be inferred from them.

11. Confidence Intervals and Precision

The primary estimate is 0.062, and its confidence interval runs from -0.042 to 0.166. That interval includes estimates on both sides of no difference. Consequently, the data do not pin down whether the event proportion was higher or lower with enriched enteral nutrition in the population represented by the trial. The estimate’s point value is only one location within a range of compatible values and should not be read as a precise measure of the underlying effect.

Precision is about the uncertainty of an estimate, not whether a result is statistically significant or clinically important. A narrow interval would restrict the range of effect sizes compatible with the data; a broader interval leaves more uncertainty. The primary interval allows for a potentially lower event proportion as well as a higher one in the enriched nutrition arm. The registry record does not specify a threshold for a clinically important difference, so the clinical importance of particular values within the interval cannot be determined from the record.

The secondary intervals also span effects in either direction: for anastomotic leakage, the risk difference is 0.008 with limits -0.060 and 0.076; for additional interventions, it is -0.044 with limits -0.127 and 0.038; and for ICU admission, it is -0.043 with limits -0.148 and 0.062. These intervals reinforce that the posted secondary estimates are uncertain, rather than establishing the absence of differences.

Confidence intervals depend on statistical assumptions and the analysis method. The registry record does not provide all details needed to evaluate those assumptions, including missing-data handling and whether any covariate adjustment was used. The posted intervals are best interpreted as the uncertainty summaries attached to the registry’s estimates, not as guarantees about the true effect.

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 illustrative sample sizes for a hypothetical future comparison, not a description of the trial’s original design calculations. For these binary outcomes, the entries are participants per arm. They do not refer to total events. The registry’s stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The 80% power column gives the participants per arm estimated to provide an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the statistical model applied. The 90% power column uses a higher target chance of detection, and therefore generally requires more participants per arm. These are planning calculations, not guarantees about what a study will find. This is not observed power.

The rows use the full observed effect and smaller fractions of that effect. As the effect being targeted becomes smaller, the planning figures rise: a smaller difference is harder to distinguish from random variation, so more participants are generally needed. The table and its associated curve should therefore be read as a sensitivity illustration: required sample size changes with the effect size chosen for planning. The figures do not establish that the observed effect is the true effect, and the registry record does not report the original sample-size assumptions used to design SANICS II.

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 = 0.218; treatment proportion p₁ = 0.280; average p̄ = 0.249.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6117 = 1.1989.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6101 = 0.5135.
4. n = (1.1989 + 0.5135)² / (0.0623)² = 756.5, rounded up to 757 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 <- 0.218045112781955                          # control proportion
p1 <- 0.28030303030303                          # 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(2175979)
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 = 757 (80% power), 1,013 (90% power)
 75% of observed effect: n per arm = 1,318 (80% power), 1,763 (90% power)
 50% of observed effect: n per arm = 2,900 (80% power), 3,881 (90% power)
power.prop.test: 756.5 
Simulated power at n = 757 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.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes in addition to the primary outcome. Testing or estimating many outcomes raises the general problem of multiplicity: even when no real effects exist, a large set of comparisons can produce findings that appear notable by chance. Researchers may address this through prespecified testing hierarchies, adjusted significance thresholds, or other procedures. The registry record does not report whether any such approach was planned or used, so the posted secondary p-values should be treated as unadjusted results rather than as multiplicity-controlled evidence.

The record does not report a prespecified hierarchy among secondary outcomes or identify which, if any, were confirmatory. It also does not provide a statistical analysis plan. Consequently, it is not possible from the registry record to determine whether the primary outcome was the only formal hypothesis test, how secondary findings were to be interpreted, or whether any analysis choices were made before outcome data were examined.

Missing-data information is also not reported in the registry record. The record does not state whether outcome information was unavailable for any participants, why data might have been missing, or how missing values were handled. These details matter because missingness can affect group comparisons, particularly if the likelihood of an unobserved outcome differs between arms or is related to the outcome itself.

The analysis population is not described. In particular, the registry record does not state whether the primary comparison included all randomized participants according to their assigned groups, or whether other exclusions or analysis sets were used. Such information is needed to assess how closely the analysis preserves the original randomized comparison. These are limits on what can be inferred from the registry record; they do not establish that the trial’s analyses were inappropriate.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: remaining serious adverse events (33.3%), anastomotic leakage (9.0%).

The registry reports serious adverse events affecting 52 participants in the standard group and 55 in the enriched enteral nutrition group. It reports other adverse events affecting 22 participants in the standard group and 16 in the enriched enteral nutrition group. Deaths are recorded for 7 participants in the standard group and 4 in the enriched enteral nutrition group. These are descriptive counts; the registry record does not provide a comparative statistical analysis for these safety summaries.

The listed top serious adverse event terms are “remaining serious adverse events” at 33.3% and “anastomotic leakage” at 9.0%. The record does not clarify in the posted summary how these term percentages were calculated or provide further event-level detail. Serious adverse events and other adverse events are separate registry categories and should not be combined or interpreted as interchangeable measures.

These counts do not establish that the intervention caused or prevented an adverse event. Assessing comparative safety requires details about event definitions, follow-up, severity, relatedness, and analysis methods; these details are not reported in the registry record. The figures are best read as the safety information posted for the two groups, with the limitations of descriptive summaries in mind.

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

The trial’s posted primary comparison does not show a clearly resolved difference in postoperative ileus between enriched enteral nutrition and standard care. The estimate favors neither a confident claim of benefit nor a confident claim of harm: its interval spans effects in either direction, and the unadjusted p-value is 0.241. This does not demonstrate that the groups are equivalent, because an uncertain estimate can remain compatible with differences that the data do not distinguish reliably.

It also does not establish that perioperative nutrition has no effect. The interval includes a range of possible effects, and the registry record does not state what magnitude would be clinically important. Without a prespecified equivalence or non-inferiority framework and its margin, a nonsignificant comparison cannot be interpreted as proof of similarity. The registry record does not report such a framework.

The secondary results offer additional comparisons but do not create a single consistent conclusion across outcomes. They are unadjusted, and the record does not describe how multiplicity was handled or provide analyses for all listed outcomes. They should therefore be interpreted cautiously and should not be used to make broader claims about recovery or complications beyond the endpoints and estimates actually posted.

Randomization is a valuable design feature for comparing groups, but a registry summary is not a complete account of trial conduct. Details about allocation procedures, missing data, analysis populations, endpoint assessment, and the prespecified statistical plan are not reported in the registry record. Those omissions constrain conclusions about the robustness of the posted comparisons. The result is best understood as an uncertain estimate from a randomized trial, not as a definitive statement about the effect of the intervention or a recommendation for clinical care.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate, a p-value, and a confidence interval answer different questions. The primary point estimate is 0.062, while the interval ranges from -0.042 to 0.166. The estimate identifies the direction and size of the observed contrast on the risk-difference scale; the interval communicates that substantial uncertainty remains; and the p-value provides a test-based summary under a null model. None should be interpreted alone.

It also demonstrates a common challenge in clinical research: a randomized comparison can still produce an imprecise estimate. Randomization supports comparability in expectation, but it does not guarantee that every estimate will be precise. Precision depends on the data and the amount of information available for the outcome. The posted interval makes clear that this comparison does not settle the direction of the underlying effect.

The record also highlights the importance of distinguishing a primary endpoint from a broad set of secondary outcomes. Multiple outcomes can be useful for describing different aspects of care, but they require a clear analysis plan if their results are to support confirmatory conclusions. Since multiplicity planning and analysis populations are not reported in the registry record, the secondary findings deserve cautious interpretation.

Finally, registry transparency affects statistical interpretation. The record provides arm-level counts and comparisons, but leaves important methodological details unreported. Readers can describe the estimates and their uncertainty while recognizing what cannot be assessed. That distinction between what the posted data show and what remains unknown is central to responsible interpretation.

18. Limitations

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

The posted record does not include the trial’s original sample-size assumptions or justification, so the planning illustrations based on the observed effect cannot be used to reconstruct the design rationale. The registry also does not report the statistical analysis plan, the precise methods used to calculate intervals and p-values, or whether the comparisons were adjusted for any baseline variables or design features.

Outcome-data completeness and analysis populations are not described. The record does not report missing-data counts or handling, exclusions, or whether the analyses followed randomized assignment. These omissions limit assessment of potential bias and of how closely the reported comparisons retain the advantages of randomization. Reasons for the difference between the enrollment figure and the outcome denominators are also not reported in the registry record.

The record lists quadruple masking but does not explain which people were masked or how masking was maintained. It does not provide details about allocation concealment, endpoint adjudication, or the measurement procedures for the primary outcome. These details matter when evaluating possible departures from the intended design, but their absence from the registry summary is not evidence that a particular problem occurred.

Only some of the listed secondary outcomes have posted numerical comparisons, and the record does not report a multiplicity strategy or hierarchy. The adverse-event information is descriptive and lacks a posted comparative analysis. In addition, the registry record does not state a threshold for a clinically important effect. These trial-specific reporting gaps mean that interpretation must remain focused on the estimates and outcome definitions that are actually recorded, rather than extending to unreported analyses or assumptions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: SANICS II Trial: Stimulation of the Autonomic Nervous System in Colorectal Surgery by Perioperative Nutrition — NCT02175979.
• Registry record last updated 2019-09-19; status last verified 2019-08.
• Results first posted 2019-09-19.
• 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.

22. Record Summary

SANICS II is recorded as a completed, multicenter, prospective, randomized, parallel-group trial comparing perioperative enriched enteral nutrition with standard care described as fasting perioperatively in colorectal surgery. The registry lists quadruple masking and enrollment of 280. The primary outcome was the number of patients developing postoperative ileus, assessed up to 3 weeks after surgery.

The posted primary counts were 29 in the standard arm and 37 in the enriched enteral nutrition arm. The risk difference was 0.062, with a confidence interval from -0.042 to 0.166 and an unadjusted p-value of 0.241. The interval leaves uncertainty about the direction of the difference.

Several secondary outcomes and adverse-event counts are also recorded, but not all listed secondary outcomes have posted analyses. Details about missing data, analysis populations, multiplicity, and the original design assumptions are not reported in the registry record. The estimates should be interpreted with those limitations in view.