Antibiotic Efficacy in Pneumonitis Following Paraffin (Kerosene) Ingestion in Children: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Antibiotic Efficacy in Pneumonitis Following Paraffin (Kerosene) Ingestion in Children (NCT01253980), a randomized na study. The primary outcome is Treatment Failure.

2. Clinical Question

The clinical setting described in the registry is paraffin ingestion followed by pneumonitis. The summary explains that paraffin ingestion accounts for many healthcare visits in the developing world, especially among children, and identifies uncertainty about whether early antibiotics affect the clinical course. The study therefore compares an antibiotic strategy with placebo in this specific circumstance. It does not address antibiotic use for other illnesses, other causes of pneumonitis, or other patient groups.

The primary outcome was assessed at routine follow-up 3 and 5 days after ingestion, or earlier if necessary. The outcome definition allowed a failure to be recorded if a participant deteriorated at any time and a change in treatment was needed. The comparison is based on the registry’s per-protocol outcome population, rather than an explicitly identified intention-to-treat population. Further details about eligibility, treatment duration, or how deviations from assigned treatment were handled are not reported in the registry record.

3. Trial Design

The study is registered as a randomized, parallel-group trial with quadruple masking. Its two listed groups received amoxicillin or placebo. The registry describes the study as placebo-controlled and states that it investigated early antibiotics in children with pneumonitis following paraffin ingestion. The registry record lists an enrollment of 74 and records the trial status as completed.

The registry gives the start as 2010-07 and primary completion as 2011-09. The sponsor is the University of Cape Town. Phase is listed as not applicable. The arm-level outcome information reports 35 participants in the placebo group and 39 in the amoxicillin group. The primary outcome is reported for the per-protocol population. These are the group counts associated with the posted outcome, not a statement about how many participants were initially assigned, treated, or included in other analyses.

The primary outcome was treatment failure, recorded as a count of participants with an event. Follow-up was scheduled at routine checks 3 and 5 days after ingestion, with assessment earlier if necessary. The registry defines failure as deterioration that necessitated a change to the treatment regimen, based on reported symptoms and clinical signs compared with the presentation assessment.

Details about the sequence-generation procedure, concealment of allocation, the exact roles included in quadruple masking, treatment duration, and adherence procedures are not reported in the registry record. The trial’s original sample-size assumptions and any planned interim analyses are also not reported in the registry record. The planning illustration associated with the posted results is a separate calculation based on the observed effect, not a record of the original design assumptions.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: per protocol

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 Treatment Failure, measured over At routine follow-up 3 and 5 days post-ingestion or earlier if necessary.

The primary endpoint is treatment failure, expressed as the number of participants who experienced an event. A participant was considered to have failed treatment if deterioration at any time required a change to the treatment regimen. The assessment drew on reported cough, shortness of breath, wheeze, and fever, together with clinical signs compared with those recorded at presentation. The signs named in the registry include respiratory rate, oxygen saturation, wheeze, flaring, grunting, recessions, crepitations, temperature, and mental status.

This endpoint is clinically interpretable as a need to alter the treatment plan following worsening, rather than as a laboratory measurement alone. Its definition brings several symptoms and signs into a single binary outcome: each participant is counted as having had treatment failure or not having had treatment failure. Because the endpoint is based on deterioration and a treatment change, the recorded result also depends on how those criteria were assessed and applied. The registry description does not report further rules for adjudication or whether outcome assessors used a standardized independent review.

The outcome was assessed at routine follow-up 3 and 5 days after ingestion, or earlier if necessary. That timing describes the period of assessment recorded for this endpoint; it should not be read as evidence about later outcomes. The per-protocol population is specified for the primary outcome. The registry record does not report secondary outcome results.

7. Results Posted in the Registry

• Amoxicillin: 5.1% (2/39) versus 8.6% (3/35) on control; risk difference -3.4 percentage points (95% CI -15.0 to 8.1), risk ratio 0.60 (0.11–3.37); unadjusted two-proportion z-test p = 0.556.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted outcome is binary: each participant either met the treatment-failure definition or did not. The outcome is reported as a count of participants with an event in each arm, alongside the number in each arm. This format makes the underlying event information visible and distinguishes the observed counts from the estimated comparison between groups. The trial’s reported analysis uses Fisher Exact and identifies relative risk as its parameter.

What does relative risk describe?

Relative risk compares the event probability in one group with the event probability in the reference group. A value of 1 represents equal event probabilities; a value below 1 represents a lower observed event probability in the intervention group, while a value above 1 represents a higher one. The sponsor-reported estimate is 0.60. Its 95% confidence interval, 0.11 to 3.37, extends across 1, so it does not isolate a direction of effect. The broad interval reflects how much uncertainty remains when the event counts are limited.

General: a relative measure describes proportional contrast, while an absolute measure describes the difference in event probability between groups. Both can be useful, but they answer different questions. A relative estimate may look substantial while the absolute event difference is small, or vice versa. For this trial, the posted recalculation includes an unadjusted risk difference as an absolute comparison. Its interval spans zero, which corresponds to no absolute difference, and reaches both negative and positive values. The posted estimate is not adjusted for other factors.

What does Fisher’s exact test do?

The registry identifies Fisher Exact as the method for the reported comparison. General: Fisher’s exact test evaluates evidence of association in a two-group categorical outcome using the observed counts, with a probability calculation that is suitable when event counts are sparse. It does not by itself express the size of the treatment contrast; the relative risk estimate and its confidence interval provide an effect-size summary. A p-value summarizes how compatible the data are with a specified null model under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure clinical importance.

The registry reports p > 0.50. The recalculation reports an unadjusted p-value of 0.556. These results both indicate that the observed counts do not provide strong statistical evidence against no difference. A large p-value does not establish that the groups are equivalent. Demonstrating equivalence would require an appropriate design and a prespecified margin for what difference would count as acceptably small; those details are not reported in the registry record.

How should a confidence interval be read?

General: a confidence interval describes the range of effect estimates compatible with the data and the method used, at the stated confidence level. It is not a guarantee that the true effect lies in the interval, and its endpoints do not represent the most extreme effects that could occur. A narrow interval indicates greater precision than a wide interval, all else equal. Here, the reported relative-risk interval is wide and includes values on both sides of 1. The recalculated risk-difference interval also includes no difference and both directions of effect. These features make the uncertainty an important part of the result, not a technical detail that can be set aside.

What is the status of the recalculation?

The recalculated comparison is a simple, unadjusted analysis from the posted group summaries. It is useful for checking the contrast implied by the event counts and for displaying an absolute effect measure alongside the reported relative measure. It is not a replacement for the sponsor’s reported analysis, which takes precedence as the trial’s own reported result. The recalculation does not add adjustment for covariates or account for participant-level information unavailable in the posted summaries. No discrepancy is recorded between the sponsor analysis and the recalculation.

General: binary outcomes can be analyzed with several methods, and methods can differ in the precise interval or p-value they produce, especially when events are sparse. The method should be interpreted together with the estimate, interval, endpoint definition, and analysis population. A single p-value cannot summarize all of those elements. In this trial, the event counts are low, the effect intervals are broad, and the primary analysis population is per protocol. Together, these registry entries call for a cautious reading of the estimated contrast.

Why do sparse events matter?

General: when events are uncommon, changing the status of a small number of participants can materially alter the estimated relative comparison. Sparse counts can produce wide intervals and make estimates sensitive to the specific data. Exact methods such as Fisher’s exact test avoid relying on some large-sample approximations for the test, but they cannot create information that the observed data do not contain. The uncertainty remains visible in the broad confidence interval. The registry record does not report additional sensitivity analyses that would show how alternative outcome or missing-data assumptions affect the estimate.

The primary outcome is described as assessed at routine follow-up 3 and 5 days after ingestion or earlier if necessary. The interval estimates apply to the posted outcome and analysis as recorded; they do not cover unreported later outcomes or alternative definitions of failure. The registry lists one primary outcome measure and one analysis, but it does not report a complete statistical analysis plan, multiplicity procedure, or detailed rules for missing outcome data. Those omissions limit what can be inferred about all planned analyses and analytic decisions.

10. Confidence Intervals and Precision

Precision is best judged from the confidence intervals, not from the point estimates alone. The sponsor-reported relative risk is 0.60, with a 95% confidence interval from 0.11 to 3.37. The interval is wide and includes 1, the value representing equal event risk between groups. As a result, the estimate does not pin down the relative effect: the data are compatible with values indicating a lower event risk in the amoxicillin group and with values indicating a higher event risk.

The unadjusted risk-difference estimate is -0.034, with a 95% confidence interval from -0.150 to 0.081. This interval includes zero and extends in both directions. It therefore allows for an absolute reduction, no difference, or an absolute increase in the event probability. The point estimate is only one location within that broad range; it should not be treated as a precise prediction.

The event counts were 3 in the placebo group and 2 in the amoxicillin group. With few events, the estimated contrast can be sensitive to the information contributed by individual outcomes. The intervals express this uncertainty more fully than the apparent difference in the counts. Neither the relative nor absolute interval demonstrates equivalence, because equivalence requires a defined margin and an analysis designed to assess that margin. Such a margin is not reported in the registry record.

General: confidence intervals quantify sampling uncertainty under the method used, but do not capture every possible source of uncertainty. They cannot account for unreported missing-data decisions, measurement differences, or limitations in applicability. The intervals should therefore be read alongside the endpoint definition, the per-protocol population, and the absence of further analysis details in the registry record.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They illustrate the number of participants per arm associated with different fractions of the observed effect and with 80% or 90% power. For example, the figures for planning around 100% of the observed effect are 844 participants per arm for 80% power and 1,129 participants per arm for 90% power. For planning around 75% of the observed effect, they are 1,588 and 2,126 participants per arm; for 50% of the observed effect, they are 3,768 and 5,044 participants per arm.

General: power is the probability that a study will detect an effect of a specified size under the assumptions used for planning, if that effect is present. The 80% column gives the illustrated per-arm size associated with an 80% chance of detecting the stated effect under those assumptions; the 90% column does the same for a 90% chance. A higher target probability generally requires more participants. Smaller effects are harder to distinguish from random variation, so the planning figures increase as the assumed effect becomes a smaller fraction of the observed effect.

The assumptions for this illustration are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect defined as the stated fraction of the observed effect. The figures are a planning illustration calculated from the observed effect, not the trial’s original design assumptions. The original sample-size justification is not reported in the registry record. These figures are not observed power.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.086; treatment proportion p₁ = 0.051; average p̄ = 0.068.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3572 = 0.7002.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3564 = 0.3000.
4. n = (0.7002 + 0.3000)² / (-0.0344)² = 843.7, rounded up to 844 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 <- 0.0857142857142857                          # control proportion
p1 <- 0.0512820512820513                          # 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(1253980)
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 = 844 (80% power), 1,129 (90% power)
 75% of observed effect: n per arm = 1,588 (80% power), 2,126 (90% power)
 50% of observed effect: n per arm = 3,768 (80% power), 5,044 (90% power)
power.prop.test: 843.7 
Simulated power at n = 844 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.

13. Analyses Reported by the Sponsor

The registry’s own reported analysis is a Fisher Exact comparison with relative risk 0.60, a 95% confidence interval from 0.11 to 3.37, and p > 0.50. That analysis is the sponsor-reported result and takes precedence as the trial’s own inferential analysis. It conveys a broad range of plausible relative effects and does not provide strong statistical evidence against no difference.

The posted recalculation uses the arm-level event summaries to give an unadjusted risk difference of -0.034, with a 95% confidence interval from -0.150 to 0.081 and p = 0.556. It is a complementary, simple recalculation rather than a substitute for the sponsor’s analysis. The risk difference presents the comparison on an absolute scale, while the sponsor’s reported relative risk presents it on a relative scale. The estimates are consistent in indicating that the observed data do not settle the direction or size of the underlying effect.

No discrepancy is recorded between the sponsor analysis and the recalculation. The methods need not produce identical numerical summaries because they describe the contrast differently and the recalculation is unadjusted. The registry record does not report additional details that would support a more extensive comparison of analytic choices.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and one analysis, and it does not list secondary posted outcomes. This makes the posted outcome set straightforward to describe, but it does not establish that no other outcomes or analyses were considered during the study. Whether multiplicity was addressed, and whether any outcomes or analyses were prespecified outside the registry record, is not reported in the registry record. No adjustment for multiple comparisons is described.

The primary endpoint is reported for the per-protocol population. This identifies the population used for the posted primary outcome, but does not explain the criteria for inclusion in that analysis or how participants who deviated from the assigned treatment were handled. An intention-to-treat analysis is not reported in the registry record. The group counts associated with the outcome do not by themselves describe all participant flow through assignment, treatment, follow-up, and analysis.

Missing-data methods are not reported in the registry record. In particular, the record does not state whether outcome data were missing, how missing outcomes were classified, or whether any imputation or sensitivity analysis was used. Those details matter because exclusion or classification of participants with unavailable outcome information can affect a per-protocol comparison.

Interim analyses and stopping rules are not reported in the registry record. The registry also does not report a full statistical analysis plan describing prespecification of the model, handling of protocol deviations, or planned sensitivity analyses. These absences should be treated as limits on what can be established from the record, rather than as evidence that a particular procedure was or was not used.

The reported p-value and confidence interval should therefore be interpreted as summaries of the posted analysis, not as a complete account of every analytical decision. The record supplies no basis for asserting an adjustment for multiplicity, a particular missing-data assumption, or a planned interim monitoring approach.

15. Safety Results

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

Other (non-serious) adverse events

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

The serious adverse event figures list 0 serious adverse events among 35 participants at risk in the placebo group and 0 among 39 participants at risk in the amoxicillin group. The listed other adverse event figures are also 0 in each group, with the same group-specific numbers at risk. No top serious adverse event terms are listed.

These figures describe the adverse-event counts recorded in the registry. They should be read as observed counts during the reporting period, not as proof that no adverse events could occur or that the treatments have identical safety profiles. With no reported events, the figures do not estimate the range of possible event risks precisely. The registry record does not provide further detail about the adverse-event collection window, event definitions, or the assessment of causality.

Deaths are not reported in the registry record. A missing value should not be interpreted as a reported count of zero. The adverse-event information is limited to the figures and categories recorded, and does not provide a complete account of all possible harms or their severity.

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

The posted results show 3 treatment failures in the placebo group and 2 in the amoxicillin group among the per-protocol outcome population. The observed counts are close, but a comparison should not rely on the counts alone. The sponsor-reported relative risk is 0.60, and its 95% confidence interval ranges from 0.11 to 3.37. The interval is wide and includes the value corresponding to equal relative risk. The unadjusted risk-difference interval also crosses zero. Both summaries leave substantial uncertainty about the direction and magnitude of any underlying difference.

These results do not establish that amoxicillin reduced treatment failure, and they do not establish that it increased treatment failure. They also do not prove that the treatments are equivalent. The registry record does not report an equivalence margin or an equivalence analysis. A p-value greater than 0.50 is not the probability that the treatments are the same; it describes the data’s compatibility with a null model under the reported test.

The conclusion applies to the defined treatment-failure endpoint and the per-protocol population recorded for the study. The endpoint depended on deterioration requiring a change to treatment, evaluated using reported symptoms and clinical signs. Follow-up for this outcome was at routine checks 3 and 5 days after ingestion or earlier if necessary. It should not be generalized to outcomes that were not posted, later follow-up, other causes of pneumonitis, or populations not described in the registry.

The posted data are informative about the observed comparison, but the small number of events and broad intervals mean that the estimate is not precise. Missing-data handling, an intention-to-treat result, and further sensitivity analyses are not reported in the registry record. Those limitations affect how confidently the result can be extended beyond the specific analysis that was posted.

17. Why This Trial Matters Statistically

This trial addresses a clear statistical problem: a binary clinical outcome with few observed events. The outcome definition combines worsening symptoms and clinical signs with a treatment change, giving the event a direct connection to the clinical course described in the registry. At the same time, the low event counts mean that the estimated contrast is uncertain. The wide relative-risk interval makes that uncertainty visible, including plausible values in both directions.

The result illustrates why an observed difference between group counts is not enough to establish a treatment effect. Estimation requires attention to the size of the contrast and the uncertainty around it. The sponsor-reported relative risk and the unadjusted absolute risk difference offer complementary descriptions, and both leave substantial room for uncertainty. The p-value alone cannot convey the possible range of effects or demonstrate equivalence.

The planning illustration also shows how the assumed effect size affects the number of participants needed in a future study under its stated assumptions. Planning for a smaller fraction of the observed effect requires more participants per arm. These calculations do not describe the original design or the trial’s power after completion; the original sample-size assumptions are not reported in the registry record.

For biostatistical interpretation, the trial is a useful example of reading sparse binary data alongside the endpoint definition, analysis population, confidence interval, and sponsor-reported test. It emphasizes that a result can be directionally suggestive while remaining too imprecise to settle the question. The registry record supports describing what was observed and how uncertain the estimates are, but not a definitive claim about benefit, harm, or equivalence.

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 primary outcome is reported for the per-protocol population, but the registry record does not explain the criteria used to define that population or provide an intention-to-treat result. Without those details, it is difficult to assess how exclusions or departures from assigned treatment may have influenced the posted comparison. Missing outcome data and their handling are not reported in the registry record.

The endpoint combines reported symptoms and clinical signs with deterioration requiring a change to the treatment regimen. The registry describes the assessment criteria, but does not report further adjudication procedures, assessor roles, or whether outcome evaluation was independently reviewed. Quadruple masking is recorded, but the identities of the masked roles are not reported in the registry record.

The event counts are limited, and the confidence intervals are wide. This constrains precision regardless of the direction of the point estimates. The registry’s posted result covers the defined treatment-failure endpoint at routine follow-up 3 and 5 days after ingestion, or earlier if necessary. Later outcomes and secondary outcomes are not posted in the registry record.

Additional information about eligibility criteria, participant characteristics, treatment duration, adherence, allocation concealment, and the randomization procedure is not reported in the registry record. The record also does not report the original sample-size justification, interim analyses, multiplicity procedures, or a full statistical analysis plan. These gaps prevent a detailed assessment of how design and analytic decisions may affect interpretation. They should be understood as limits of the registry information, not as evidence that any specific practice was absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Antibiotic Efficacy in Pneumonitis Following Paraffin (Kerosene) Ingestion in Children — NCT01253980.
• Registry record last updated 2015-11-09; status last verified 2015-10.
• Results first posted 2013-06-26.
• 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

NCT01253980 is a completed randomized, parallel-group, placebo-controlled trial sponsored by the University of Cape Town. It studied amoxicillin versus placebo for children with pneumonitis following paraffin (kerosene) ingestion. The registry records quadruple masking, enrollment of 74, a start of 2010-07, and primary completion of 2011-09.

The primary endpoint was treatment failure in the per-protocol population, assessed at routine follow-up 3 and 5 days after ingestion or earlier if necessary. The posted results record 3 failures in the placebo group and 2 in the amoxicillin group. The sponsor-reported relative risk is 0.60, with a 95% confidence interval from 0.11 to 3.37 and p > 0.50. The interval is broad, and the posted results do not resolve the direction or size of any underlying difference.

The registry record does not report secondary outcome results, missing-data methods, an intention-to-treat analysis, the original sample-size assumptions, or interim analyses. The results should be interpreted in light of the endpoint definition, per-protocol population, limited event counts, and uncertainty of the estimates.