Dilute Povidone-iodine Irrigation vs No Irrigation for Children With Acute, Perforated Appendicitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dilute Povidone-iodine Irrigation vs No Irrigation for Children With Acute, Perforated Appendicitis (NCT02664220), a randomized phase 2 study. The primary outcome is Number of Participants With Postoperative Intra-abdominal Abscess.

2. Clinical Question

The question is clinically focused on a postoperative complication in children undergoing surgery for perforated appendicitis. The primary endpoint records participants with a confirmed abscess, rather than describing abscess severity or the time until an abscess occurred. Confirmation was based on imaging using a standardized definition and protocol, as stated in the endpoint description.

The registry record lists a randomized, parallel-group comparison and reports the primary outcome in both groups. It also lists hospital length of stay, hospital readmission, and emergency-room visits as secondary outcomes, each with a 30-day post-surgery timeframe. These outcomes broaden the description of postoperative care but do not replace the primary question. The posted results are descriptive evidence from this pilot trial; interpretation depends on both the observed group differences and their statistical uncertainty.

3. Trial Design

The registry record describes a randomized, single-masked, parallel-group phase 2 pilot trial. The listed enrollment is 100, with 50 participants reported in each arm. The groups are povidone-iodine irrigation and no irrigation. The record identifies The University of Texas Health Science Center, Houston as the sponsor and lists the trial status as completed. The study start is recorded as 2016-04 and primary completion as 2018-03.

The trial’s stated purpose was to compare PVI irrigation with no irrigation for decreasing postoperative intra-abdominal abscesses in children with perforated appendicitis. The summary also identifies safety verification as an aim. The registry record does not identify who was masked, nor does it provide fuller details of the irrigation procedure, the surgical care protocol, or other co-interventions. Those details are not reported in the registry record.

The primary outcome is the number of participants with a postoperative intra-abdominal abscess by 30 days post surgery. The secondary outcomes are total hospital length of stay, hospital readmission, and emergency-room visits, also assessed over the stated 30-day post-surgery timeframe. The registry lists four outcome measures in total, but its record of reported analyses does not include analysis descriptions for the secondary outcomes.

Randomization is intended to create comparable groups, on average, with respect to factors that might affect outcomes. It does not guarantee that small groups will be balanced on every factor, and the registry record does not provide baseline characteristics or details of the randomization procedure. Allocation concealment, the specific masking procedure, and the trial’s original sample-size justification are not reported in the registry record. The enrollment figure alone should therefore not be taken as evidence about the planned precision or statistical power of the trial.

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.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Postoperative Intra-abdominal Abscess, measured over 30 days post surgery.

The primary endpoint counts participants with a postoperative intra-abdominal abscess by 30 days post surgery. The registry description says that an abscess was confirmed by imaging, using a standardized definition and protocol. The outcome is therefore a participant-level event count: it records whether a participant met the endpoint, rather than how many abscesses a participant experienced or how severe an abscess was.

This endpoint addresses the trial’s central question because the stated aim was to compare irrigation with no irrigation for decreasing postoperative intra-abdominal abscesses. A clearly defined, imaging-confirmed outcome can support more consistent classification across participants than an outcome based only on a less standardized clinical impression. The registry description, however, does not report further information about image review, adjudication, or the handling of uncertain findings.

The reported group counts are 6 participants in the povidone-iodine irrigation arm and 8 in the no-irrigation arm, with 50 participants reported in each arm. These counts are the observed endpoint data. They do not, by themselves, establish a difference between the groups: the comparison must also account for the uncertainty expected when event counts are limited. The estimate and confidence interval describe that uncertainty. The endpoint’s 30-day timeframe also means the result addresses the registry’s stated follow-up window, not outcomes beyond that period.

7. Results Posted in the Registry

• No Irrigation: 16.0% (8/50) versus 12.0% (6/50) on control; risk difference 4.0 percentage points (95% CI -9.6 to 17.6), risk ratio 1.33 (0.50–3.56); unadjusted two-proportion z-test p = 0.564.

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.

Total Hospital Length of Stay

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • No Irrigation: mean 6.10 versus 5.10 on control; difference 1.00 (95% CI -0.13 to 2.13), standardized effect d = 0.35; z-test p = 0.083.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Irrigation and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Were Readmitted to the Hospital

• 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:
  • No Irrigation: 6.0% (3/50) versus 0.0% (0/50) on control; risk difference 6.0 percentage points (95% CI -0.6 to 12.6); unadjusted two-proportion z-test p = 0.079.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Irrigation and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Visited the Emergency Room

• 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:
  • No Irrigation: 14.0% (7/50) versus 6.0% (3/50) on control; risk difference 8.0 percentage points (95% CI -3.7 to 19.7), risk ratio 2.33 (0.64–8.51); unadjusted two-proportion z-test p = 0.182.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between No Irrigation and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context about postoperative recovery and health-care use, but they do not provide a more definitive answer to the primary abscess question. In the posted results, the group contrasts generally point toward lower event counts or a shorter average stay in the irrigation group, while the uncertainty intervals for the comparisons include no difference. The outcomes therefore do not form a consistent body of precise evidence that resolves the primary comparison.

These measures capture different aspects of the postoperative course. Length of stay is a continuous measure of time in hospital; readmission and emergency-room visits are participant-level event counts. They may be related to postoperative complications, but they are not interchangeable with imaging-confirmed abscesses. A participant could have an abscess without a particular health-care visit, or require care for another reason. The registry does not report the relationships between these outcomes at the participant level.

The registry lists these outcomes as secondary and reports unadjusted comparisons. When several outcomes are examined, the chance of observing an apparently notable result by chance can increase. Without a reported multiplicity strategy, secondary p-values should be treated as exploratory rather than as independent confirmatory evidence. The registry record does not report a prespecified hierarchy among the secondary outcomes or whether any adjustment was planned.

Overall, the secondary results can help describe the observed postoperative course, but they should be interpreted in light of their uncertainty, their distinct definitions, and their secondary status. They do not remove the uncertainty around the primary endpoint or establish that one treatment strategy changes recovery or health-care use.

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

• Total Hospital Length of Stay
• Number of Participants Who Were Readmitted to the Hospital
• Number of Participants Who Visited the Emergency Room

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, the registry reports participant counts in each arm and a risk-difference comparison. A risk is the proportion of participants in a group who experience the outcome. The risk difference expresses the comparison as the risk in the no-irrigation group minus the risk in the irrigation group. A value above zero therefore indicates a higher observed risk in the no-irrigation group; a value below zero indicates a higher observed risk in the irrigation group. The posted estimate is 0.04. This is an absolute-scale comparison, not a relative multiplier.

The confidence interval for the risk difference runs from -0.096 to 0.176. It represents a range of values compatible with the observed data under the statistical method used and its assumptions. Because the range includes zero, the data are compatible with no difference as well as with differences in either direction. The interval’s width is important: it shows that the estimate is not precise enough to narrow the plausible differences substantially. Confidence intervals do not assign a probability to a particular treatment effect, and they do not guarantee that the true effect lies inside the interval.

The registry also reports a risk ratio and an odds ratio for the primary comparison. A risk ratio compares the risks by division, while an odds ratio compares the odds of the outcome. Both are relative measures, unlike the risk difference. Their interpretation depends on which group is used as the reference; the posted comparison is no irrigation relative to irrigation. The risk ratio is 1.333 and the odds ratio is 1.397. Their confidence intervals, 0.499 to 3.564 and 0.447 to 4.367 respectively, are wide and include the value corresponding to no relative difference. Relative measures can look different in scale from absolute measures, so they should be read alongside the observed counts and the risk difference.

The unadjusted p-value for the primary comparison is 0.564. In general, a p-value describes how unusual data at least as incompatible 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 is it a measure of clinical importance. A p-value should be interpreted with the effect estimate and confidence interval, not used as a stand-alone verdict. The posted p-value is unadjusted; the registry record does not report a multiplicity adjustment.

Hospital length of stay is a continuous outcome, reported as a mean and standard deviation for each arm. The comparison is a mean difference: the no-irrigation mean minus the irrigation mean. The posted difference is 1.0 day, with a confidence interval from -0.131 to 2.131 and an unadjusted p-value of 0.083. A mean difference summarizes the average contrast, but it does not describe the full distribution of length of stay. The standard deviations show variation among participants within each group. In general, substantial variation relative to a group difference makes that difference harder to estimate precisely.

Readmission and emergency-room visits are also binary outcomes, reported as counts of participants with each event. Their estimates are risk differences, with no-irrigation minus irrigation as the comparison. The readmission estimate is 0.06, with a confidence interval from -0.006 to 0.126 and an unadjusted p-value of 0.079. The emergency-room-visit estimate is 0.08, with a confidence interval from -0.036 to 0.197 and an unadjusted p-value of 0.182. For sparse event counts, estimates can be especially uncertain; a small change in the observed count can materially affect the comparison. General statistical methods for sparse data may use approaches tailored to that setting, but the registry does not report the method used for these analyses.

In general, random allocation helps reduce confounding by balancing known and unknown prognostic factors across groups in expectation. It does not ensure balance in a pilot trial, and the record does not provide baseline data with which to assess the achieved balance. The posted registry record lists no analysis descriptions for the primary comparison and no reported analysis descriptions for the secondary outcomes. It is therefore not possible to determine from the record whether any adjusted models, alternative tests, or sensitivity analyses were performed. The posted comparisons should be read as the estimates recorded, without inferring an unreported analysis procedure.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a comparison. The primary risk-difference estimate is 0.04, but its confidence interval extends from -0.096 to 0.176. Because the interval crosses zero, the posted data are compatible with a higher risk in either group as well as no difference. The interval also spans a range of potentially meaningful differences, so the point estimate alone gives an incomplete picture.

The relative estimates are similarly uncertain. The risk-ratio interval extends from 0.499 to 3.564, while the odds-ratio interval extends from 0.447 to 4.367. Both include the value corresponding to no relative difference. The broad ranges reflect limited precision in the comparison; they should not be read as evidence that all values within them are equally likely or as a guarantee about the true effect.

The secondary outcome intervals also indicate uncertainty. The hospital-length-of-stay mean-difference interval runs from -0.131 to 2.131 days. The readmission risk-difference interval runs from -0.006 to 0.126, and the emergency-room-visit risk-difference interval runs from -0.036 to 0.197. Each includes zero, so each is compatible with no difference. These intervals also permit differences in either direction, with varying ranges across outcomes.

Confidence intervals are most informative when considered alongside the point estimates, outcome definitions, and design. Here, the reported event counts are modest and the study is designated a pilot. The resulting uncertainty means that the estimates should not be treated as precise evidence for a particular effect size. The registry record does not report a prespecified precision target or the trial’s original sample-size assumptions, so the reported intervals are the clearest guide to the precision of the posted comparisons.

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 of the participants per arm that would be needed under the stated assumptions to detect specified fractions of the observed effect. They are not a report of the trial’s original design calculation, and they are not observed power. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

The 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 set to the stated fraction of the observed effect. For the binary outcomes, the entries refer to participants per arm; for time-to-event outcomes, the stated convention would instead be total events. The outcomes in this trial are not time-to-event outcomes, so the relevant planning entries are participants per arm.

The 80% power column gives the illustrative participants per arm for a design that would have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect. The 90% power column uses a higher chance of detection under the same general planning framework. These are design calculations, not probabilities that the observed result is correct and not a description of the power achieved by this trial.

For the primary endpoint, the planning entries are 1,181 participants per arm for 80% power and 1,580 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, they are 2,036 and 2,725; for 50% of the observed effect, they are 4,438 and 5,940. The direction of the pattern is expected: smaller effects are harder to detect and require more participants. The posted planning figures for the other outcomes are likewise illustrations based on their observed effects, not guarantees about future study results.

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 = 0.120; treatment proportion p₁ = 0.160; average p̄ = 0.140.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4907 = 0.9618.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4899 = 0.4123.
4. n = (0.9618 + 0.4123)² / (0.0400)² = 1,180.1, rounded up to 1,181 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 <- 0.12                          # control proportion
p1 <- 0.16                          # 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(2664220)
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 = 1,181 (80% power), 1,580 (90% power)
 75% of observed effect: n per arm = 2,036 (80% power), 2,725 (90% power)
 50% of observed effect: n per arm = 4,438 (80% power), 5,940 (90% power)
power.prop.test: 1180.1 
Simulated power at n = 1,181 per arm: 0.805 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary outcome and lists three secondary outcomes. It reports unadjusted comparisons, but does not report a multiplicity adjustment or a procedure for controlling the chance of false-positive findings across outcomes. When multiple outcomes are tested, each additional comparison can increase the opportunity for a chance finding. This is why unadjusted secondary results generally carry less confirmatory weight than a prespecified primary result. The record does not report whether the investigators planned a particular hierarchy or other approach to multiplicity.

Missing-data procedures are not reported in the registry record. The posted outcome summaries do not explain whether all randomized participants contributed data to every outcome, whether any values were missing, how missing outcomes were handled, or whether any sensitivity analyses were performed. It is not appropriate to assume that there were no missing data simply because group denominators are listed.

The analysis populations are also not reported in the registry record. In particular, the record does not say whether the primary comparison followed an intention-to-treat approach, used a per-protocol population, or relied on another definition. The group counts and denominators describe the posted results, but do not establish which participants were included under a formal analysis-population rule.

The registry lists zero analysis descriptions for the primary outcomes and no reported analyses for the secondary outcomes. It therefore does not document the statistical tests or models used, adjustments for baseline factors, prespecified subgroup analyses, or sensitivity analyses. The available comparisons can be described as posted, unadjusted estimates, but the record does not permit a fuller assessment of the analysis plan or its implementation.

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.

The registry reports zero serious adverse events and zero deaths in each arm. It also reports zero other adverse events in each arm. For each safety category, the number at risk is recorded as 50 in the povidone-iodine irrigation group and 50 in the no-irrigation group.

These figures mean that no adverse events in the listed categories were recorded in the registry results for either group. They do not establish that the intervention is free of risk. The record does not provide detailed adverse-event definitions, surveillance procedures, event severity beyond the serious/non-serious categories, or information about how long adverse events were followed. The serious-event terms list is empty, consistent with the reported absence of serious events.

Safety interpretation should consider the scope of the recorded follow-up and the size of the trial. With no reported events, a comparative safety estimate cannot meaningfully characterize uncommon harms. The registry’s stated safety aim is not, by itself, evidence that safety was established. These event counts describe what was recorded; they do not support broader claims about safety in other populations or settings.

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

The posted results provide an estimate of the difference in postoperative abscess counts between the randomized groups during the 30 days post surgery. The observed counts were lower in the irrigation group, but the estimated risk difference is imprecise and its confidence interval includes no difference as well as differences in either direction. The relative estimates are also uncertain. The central statistical message is therefore that the trial does not precisely resolve the primary comparison.

This is not the same as showing that the groups are equivalent. To establish that differences are small enough to be considered practically unimportant would require a prespecified equivalence or non-inferiority framework and a sufficiently precise interval around an appropriate margin. No such margin or analysis is reported in the registry record. Nor does an unadjusted p-value above a conventional threshold prove there is no effect.

The findings also do not establish that irrigation works or does not work. A randomized design supports a comparative interpretation, but the estimates remain limited by their uncertainty, and the record lacks detail on several aspects of the protocol and analysis. Results from a pilot trial can inform the design and planning of further research, but the observed effect in a small trial may be an unstable guide to the effect that would be seen in a larger study.

The secondary outcomes provide additional descriptions of length of stay and health-care visits. They do not resolve the primary endpoint, and their unadjusted nature and uncertainty limit the strength of conclusions drawn from them. The adverse-event record reports no events in the listed categories, but this does not establish absence of harm. Overall, the registry record documents observed outcomes and uncertain comparisons in this trial; it does not settle the clinical question or justify extrapolation beyond the studied population and follow-up.

17. Why This Trial Matters Statistically

This trial illustrates why group counts, effect estimates, and uncertainty intervals need to be considered together. A difference between observed counts is not, on its own, evidence of a reliable treatment effect. The risk-difference estimate communicates the absolute contrast, while relative measures communicate the comparison on another scale. The confidence intervals show how much uncertainty remains around each estimate.

The primary interval is compatible with no difference and with effects in either direction. That pattern is a useful reminder that failure to obtain a precise distinction between groups is not proof that the interventions are equivalent. It also shows why reporting only a p-value or only the point estimate would leave out important information. Readers need to understand both the estimated contrast and the range of uncertainty.

The pilot setting is also relevant statistically. Pilot trials can provide practical information and initial estimates, but effect estimates based on limited data may be unstable. Planning calculations based on the observed effect are especially sensitive to that uncertainty: they illustrate assumptions for future designs, rather than revealing the trial’s achieved power or confirming that the observed effect will recur.

Finally, the registry record shows the importance of transparent reporting. It provides group counts and outcome comparisons, but does not report key details such as the original sample-size justification, missing-data handling, analysis populations, or multiplicity procedures. Those omissions constrain assessment of how the results were generated and how confidently they can be interpreted. Clear reporting of methods alongside estimates is essential for judging what a clinical trial can and cannot establish.

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.

Several limitations specific to this trial affect interpretation. The study is designated a pilot trial, and the primary comparison is based on a limited number of observed abscess events. The confidence interval is broad, so the estimate does not tightly identify the size or direction of a difference. The posted counts should not be treated as a precise estimate of what would occur in a broader population.

The registry record provides limited detail about trial conduct. It does not report the full eligibility criteria, randomization procedure, allocation concealment, which party was masked, or fuller descriptions of the treatment protocols. The arm descriptions are empty. Baseline characteristics are not reported in the outcome details, so the achieved balance of prognostic factors cannot be assessed from this record.

Important analysis details are also absent. The record does not report the original sample-size assumptions, missing-data handling, formal analysis populations, statistical methods, or multiplicity procedures. It does not report whether adjusted or sensitivity analyses were conducted. The posted secondary comparisons are unadjusted, and the record does not state whether their analysis was prespecified.

Follow-up for the primary endpoint and listed secondary outcomes is framed around 30 days post surgery. The registry record does not provide results beyond that timeframe. The safety results list no events in the recorded categories, but the record does not describe adverse-event ascertainment in detail. These limitations do not invalidate the posted results; they restrict the strength, scope, and precision of conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dilute Povidone-iodine Irrigation vs No Irrigation for Children With Acute, Perforated Appendicitis — NCT02664220.
• Registry record last updated 2019-04-17; status last verified 2019-03.
• Results first posted 2019-04-17.
• 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

NCT02664220 is a completed, randomized, single-masked, parallel-group phase 2 pilot trial sponsored by The University of Texas Health Science Center, Houston. It compared povidone-iodine irrigation with no irrigation for children with acute, perforated appendicitis. The registry lists enrollment of 100 and records the study start as 2016-04 and primary completion as 2018-03.

The primary outcome was participants with a postoperative intra-abdominal abscess by 30 days post surgery, confirmed by imaging using a standardized definition and protocol. The reported counts were 6 in the irrigation group and 8 in the no-irrigation group. The risk-difference estimate was 0.04, with a confidence interval from -0.096 to 0.176 and an unadjusted p-value of 0.564.

Secondary outcomes covered hospital length of stay, readmission, and emergency-room visits. Their comparisons were also unadjusted and uncertain. The registry reports no serious adverse events, other adverse events, or deaths in either group. Important details of the original design and statistical analysis are not reported in the registry record, limiting conclusions beyond the posted estimates and follow-up.