Amoxicillin Versus Benzyl Penicillin for Treatment of Children Hospitalised With Severe Pneumonia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Amoxicillin Versus Benzyl Penicillin for Treatment of Children Hospitalised With Severe Pneumonia (NCT01399723), a randomized phase 3 study. The primary outcome is Treatment Failure at 48 Hours (Two Full Days After Enrollment).

2. Clinical Question

The primary endpoint counts participants who meet a treatment-failure criterion by 48 hours after enrollment. The trial is described as randomized and open label, so allocation was random but masking was absent. The central comparison is therefore between assigned treatment groups, using the primary endpoint within the stated intention-to-treat population.

The registry lists treatment failure, readmission, death, and a day-14 death-or-readmission outcome among its outcome measures. The posted results include the primary 48-hour outcome and selected later outcomes. The question is about comparative outcomes in this trial population; it does not by itself establish what would happen in other settings or populations.

3. Trial Design

This is a phase 3, randomized, open-label, parallel-group clinical trial of amoxicillin versus benzyl penicillin for severe childhood pneumonia among inpatients. The registry lists an enrollment of 561 and a completed status. The recorded study dates are 2011-09 for start and 2013-09 for primary completion.

Participants were assigned to amoxicillin or benzyl penicillin. The arm information describes amoxicillin as 45mg/kg 12 hourly and benzyl penicillin as 50,000IU/kg 6 hourly. The study’s brief summary frames the comparison as initial treatment with oral amoxicillin against benzyl penicillin, described there as the current standard. The registry does not report further details of the randomization procedure, allocation concealment, or treatment adherence.

Masking is listed as none. In an open-label study, treatment assignment is not concealed from participants or study personnel after allocation. That can matter particularly for outcomes involving clinical assessment or decisions about revising antibiotic treatment. The registry does not report how outcome assessors were masked, nor does it provide further procedures for limiting assessment bias.

The primary endpoint is treatment failure at 48 hours, with the analysis population identified as intention to treat. The posted primary arm results list 263 participants in each group. Those outcome denominators and the registry’s enrollment figure are distinct entries; the reason for any difference between them is not reported in the registry record. The protocol’s original sample-size assumptions, including any non-inferiority margin used in planning, are also not reported in the registry record.

Secondary outcomes include treatment failure by discharge or day 5, readmission with severe or very severe pneumonia within 14 days, death through five days, and the day-14 death-or-readmission outcome. Results are posted for treatment failure by discharge or day 5 and for the day-14 composite. Separate results for readmission and death are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat analysis

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 at 48 Hours (Two Full Days After Enrollment), measured over 48 hours.

The primary endpoint is the number of participants with treatment failure at 48 hours, described as two full days after enrollment. The population for the posted primary analysis is intention to treat. This endpoint is intended to capture early clinical deterioration or another event indicating that the assigned initial antibiotic treatment was not sufficient without a change in management.

The registry definition includes development of signs of very severe pneumonia; hypoxemia, defined as SpO2 below 85% or below 80% according to the altitude category; persistent vomiting that prevents retention of amoxicillin after repeated administration attempts; and a clinical diagnosis of a new bacterial co-morbid condition requiring revision of antibiotic treatment. It also includes lower chest wall indrawing, temperature at least 38°C, and a respiratory rate at least 5bpm above the admission rate when that rate is already above the age-adjusted normal upper limit.

Using a binary event endpoint makes the comparison interpretable as the proportion of participants who experienced treatment failure by the specified time. A fixed early assessment can capture prompt failures while keeping the outcome tied to a defined interval after enrollment. The clinical components are not identical in severity or subjectivity, however, and the registry does not report how each component was adjudicated or how disagreements were resolved.

The endpoint is useful for evaluating the trial’s stated non-inferiority question because it compares the frequency of an unfavorable outcome between assigned treatments. The registry’s classification of the sponsor analysis as non-inferiority or equivalence does not, on its own, establish the decision criterion: the non-inferiority margin and its prespecified application are not reported in the registry record.

7. Results Posted in the Registry

• Penicillin: 8.0% (21/263) versus 7.6% (20/263) on control; risk difference 0.4 percentage points (95% CI -4.2 to 5.0), risk ratio 1.05 (0.58–1.89); unadjusted two-proportion z-test p = 0.871.

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.

Treatment Failure at or Before Discharge / Day 5 Post Enrollment (Whichever Occurs First)

• 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:
  • Penicillin: 11.0% (29/263) versus 11.4% (30/263) on control; risk difference -0.4 percentage points (95% CI -5.8 to 5.0), risk ratio 0.97 (0.60–1.56); unadjusted two-proportion z-test p = 0.890.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Penicillin and the control. The interval gives the range of effects that remain compatible with the data.

Outcome (Death/Readmission) at 14 Days as Determined by Telephone or Direct Interview

• 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:
  • Penicillin: 16.8% (42/250) versus 13.5% (33/244) on control; risk difference 3.3 percentage points (95% CI -3.0 to 9.6), risk ratio 1.24 (0.82–1.89); unadjusted two-proportion z-test p = 0.310.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Penicillin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results add context about outcomes beyond the primary 48-hour endpoint. The posted measures include treatment failure by discharge or day 5 and a day-14 composite of death or readmission. Across these measures, the observed comparisons do not present a uniformly decisive separation between assigned groups. This general pattern is compatible with the primary result’s uncertainty, but it does not independently establish the primary non-inferiority question.

These outcomes differ in what they capture and when they are assessed. Treatment failure by discharge or day 5 extends beyond the primary 48-hour window, while the day-14 composite incorporates later events and follow-up by telephone or direct interview. A later composite cannot be treated as another measurement of the same endpoint: its event definition, observation period, and available participants differ.

The registry also lists readmission within 14 days and death through five days as separate secondary outcomes, but separate results for those outcomes are not reported in the registry record. The death-or-readmission composite does not show which component accounts for the observed composite events. Interpretation of the components separately is therefore limited.

Unadjusted secondary comparisons carry less weight than a prespecified primary comparison when many outcomes are examined. With multiple outcomes, some apparent differences can arise by chance, and the registry does not report a multiplicity adjustment or a hierarchy for secondary hypotheses. Secondary results are consequently most useful as descriptive or supportive context. They should not be treated as confirmatory evidence without a stated analysis plan and appropriate control of the overall testing process.

The outcome denominators also vary across posted measures. The registry does not report why follow-up availability differs or how missing outcomes were handled. That limits direct comparisons across endpoints and makes it difficult to determine whether the observed secondary pattern could be affected by incomplete ascertainment.

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

• Treatment Failure at or Before Discharge / Day 5 Post Enrollment (Whichever Occurs First)
• Readmission With Diagnosis of Severe or Very Severe Pneumonia Within 14 Days of Enrollment
• Death at or Before Five Days Following Enrollment
• Outcome (Death/Readmission) at 14 Days as Determined by Telephone or Direct Interview

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the treatment-failure definition by 48 hours or did not. For a binary endpoint, the event count and the number assessed in each group allow the event proportion to be described. The posted primary counts are 20 of 263 for amoxicillin and 21 of 263 for penicillin. The corresponding proportions in the recalculation are 0.076 and 0.080.

What does a risk difference express?

A risk difference subtracts one group’s event proportion from the other group’s event proportion. It is an absolute comparison, so it describes how far apart the two event proportions are on the probability scale. The recalculated estimate is 0.004, with penicillin as the comparison relative to amoxicillin. A positive value under that orientation means the observed event proportion is higher in the comparison group; reversing the group order reverses the sign. The sign therefore cannot be interpreted without knowing the direction of the contrast.

The registry also lists relative measures for the primary comparison: a risk ratio of 1.05 with an interval from 0.583 to 1.89, and an odds ratio of 1.054 with an interval from 0.557 to 1.995. A risk ratio compares event proportions as a ratio, while an odds ratio compares the odds of an event. These measures answer different questions from the risk difference and have different scales. Their intervals are broad enough to include values corresponding to different possible comparative patterns, so they should not be reduced to their point estimates alone.

How should the confidence interval be read?

A confidence interval communicates the uncertainty around an estimate under the statistical procedure used. It gives a range of values compatible with the data and that procedure; it is not a guarantee that the true effect lies inside the particular interval. The primary recalculated 95% confidence interval runs from -0.042 to 0.050. Because it spans zero, it includes no difference as well as values in both directions. That does not establish equivalence. For a non-inferiority analysis, the interval must be assessed against a prespecified margin, and that margin is not reported in the registry record.

What does the p-value contribute?

The unadjusted p-value for the primary recalculation is 0.871. A p-value describes how compatible the observed data are with a specified null model under the test’s assumptions; it is not the probability that the null hypothesis is true, nor does it measure the probability that the treatments are equivalent. A large p-value does not prove the absence of a meaningful difference. It must be read alongside the effect estimate, its confidence interval, and the clinical and design criteria for the trial question.

The sponsor’s reported primary result is expressed as a risk difference of -0.4 with a 95% confidence interval from -5.0 to 4.2. The registry identifies it as a non-inferiority or equivalence result but leaves the method field blank. The recalculation is a simple, unadjusted analysis of the posted summary statistics. Since the analysis specifications and non-inferiority margin are not reported, the sponsor’s inferential conclusion cannot be reconstructed from the summary alone.

Why does the intention-to-treat population matter?

An intention-to-treat analysis compares participants according to their randomized assignments, rather than reassigning them according to treatment received. This approach generally preserves the basis of randomized comparison, though its practical implementation depends on outcome availability and the analysis rules. The registry names intention to treat for the primary endpoint, but does not report how missing outcomes, crossovers, or deviations from assigned treatment were handled. It is therefore not possible to tell from the record whether every randomized participant contributed an observed endpoint or how unavailable outcomes entered the analysis.

The study is open label, so the assignment was not masked. Randomization can help balance measured and unmeasured characteristics on average, but it does not prevent bias in outcome assessment or treatment decisions after assignment. This is relevant because some components of treatment failure involve clinical diagnosis or decisions about revising antibiotic treatment. The registry does not report details about blinded adjudication or safeguards against differences in assessment.

Finally, recalculations from posted counts do not reproduce all possible features of the sponsor’s analysis. Adjustment, a specific interval method, handling of missing data, or other prespecified procedures could alter inferential results. The registry’s method field is not reported, so such details should not be assumed. The recalculated risk difference, interval, and p-value are best read as transparent unadjusted summaries alongside, rather than in place of, the sponsor’s reported analysis.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.004, and its 95% confidence interval extends from -0.042 to 0.050. This interval is broad enough to include no difference and values favoring either group under the recalculation’s comparison orientation. The point estimate is close to zero, but precision is judged from the range of values compatible with the data, not from the point estimate alone.

The sponsor’s reported risk difference is -0.4, with a 95% confidence interval from -5.0 to 4.2. The registry does not state the method used to construct this interval or the non-inferiority margin. Without those details, the interval can be described but not assessed against the trial’s non-inferiority decision boundary. Its inclusion of values in both directions also means that the summary does not show a precisely determined single direction of difference.

Confidence intervals are not a measure of clinical importance by themselves. A reader needs an appropriate clinical threshold, and for non-inferiority an explicit margin, to judge whether uncertainty is acceptably small. Neither the margin nor its justification is reported in the registry record. The available intervals therefore support a description of statistical uncertainty, but do not settle whether the range is clinically acceptable for the trial’s intended decision.

The secondary confidence intervals are also relevant context, but they concern different outcomes and follow-up periods. Their precision should be considered separately, especially for the day-14 outcome, whose posted group denominators differ from those for the primary endpoint. The reasons for those denominators and the handling of missing follow-up are not reported.

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 participants per arm, not total events. They are illustrations based on the observed effect, rather than the trial’s original design calculation. The 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 original design assumptions for this trial, including its own target effect and any non-inferiority margin, are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have 80% power under those assumptions if the selected effect were the true effect. The 90% power column gives the corresponding number for a design targeting 90% power. Power is a planning probability under specified assumptions; it is not a probability that the trial’s conclusion is correct.

The rows planning for 100%, 75%, and 50% of the observed effect illustrate how the target effect changes the required sample size. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. The figures are especially sensitive when the observed effect is small, and should not be interpreted as an estimate of the actual sample size needed for a future study without suitable design assumptions.

These calculations are not observed power. They are planning illustrations derived from the observed effect and the stated assumptions. They do not tell whether the completed trial had adequate power under its actual design, because the original design assumptions are not reported. The displayed curve should be understood in the same planning context: it represents how the illustration changes with the effect used, not a post-trial measure of certainty.

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 = 0.076; treatment proportion p₁ = 0.080; average p̄ = 0.078.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3791 = 0.7431.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3791 = 0.3191.
4. n = (0.7431 + 0.3191)² / (0.0038)² = 78,036.3, rounded up to 78,037 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 <- 0.0760456273764259                          # control proportion
p1 <- 0.0798479087452472                          # 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(1399723)
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 = 78,037 (80% power), 104,468 (90% power)
 75% of observed effect: n per arm = 137,958 (80% power), 184,686 (90% power)
 50% of observed effect: n per arm = 308,660 (80% power), 413,208 (90% power)
power.prop.test: 78036.3 
Simulated power at n = 78,037 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary result is reported as a risk difference of -0.4 with a 95% confidence interval from -5.0 to 4.2. The registry classifies the analysis as non-inferiority or equivalence. It does not report a p-value for that analysis, identify the method, or state the non-inferiority margin.

The simple recalculation from the posted primary counts gives a risk difference of 0.004 for penicillin relative to amoxicillin, with a 95% confidence interval from -0.042 to 0.050 and an unadjusted p-value of 0.871. This recalculation is unadjusted and uses the event counts and denominators shown for the arms; it is not necessarily methodologically identical to the sponsor’s analysis.

Risk-difference signs depend on which arm is subtracted from which, and the two displays use different numerical scales. A reversal in contrast order changes the sign, while a change of scale changes the numerical representation. The registry does not describe the sponsor’s method or make its contrast orientation explicit, so exact numerical reconciliation is not possible from the record alone.

The registry reports no discrepancy flag. The sponsor’s reported analysis remains the trial’s own inferential result, while the recalculation serves as a transparent check based on posted summary statistics. Neither should be interpreted as confirming non-inferiority without the margin and analysis rule used for that judgment.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, including separate readmission and death outcomes and a day-14 death-or-readmission composite. It does not report whether the analyses were arranged in a prespecified testing hierarchy, whether the secondary tests were adjusted for multiplicity, or whether the sponsor used another method to control the chance of false-positive findings across outcomes. Those details are not reported in the registry record.

Multiplicity matters because repeated testing across outcomes can increase the chance that at least one result appears statistically notable by chance, even when there is no corresponding underlying difference. This does not make secondary results unusable, but it affects how strongly they should support a confirmatory claim. In the absence of a reported adjustment or hierarchy, secondary comparisons should be treated as exploratory or descriptive rather than as independent confirmation of the primary result.

The primary analysis population is identified as intention to treat. However, the registry does not report the handling of missing primary outcomes, participants who did not follow assigned treatment, or any imputation or sensitivity analyses. It also does not explain the differences in posted denominators across the day-14 outcome and the primary outcome. The day-14 measure specifies telephone or direct interview, but the record does not describe the success of follow-up or how unavailable interviews were addressed.

These omissions matter because an intention-to-treat label does not by itself explain how missing outcome data were incorporated. The treatment groups can only be compared as intended if outcome availability and analysis rules are sufficiently clear. Without those details, readers cannot assess the influence of missingness or verify that the sponsor’s analysis followed the randomized assignment for every participant.

The registry also does not report a protocol-level statistical analysis plan, the non-inferiority margin, interim analyses, or the rationale for the original sample size. No inference should be made about these design choices from the posted summaries. Their absence limits the ability to evaluate prespecification, multiplicity control, and the exact criteria used to interpret non-inferiority.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: congestive heart failure (0.4%), hypovolemic shock (0.4%), renal failure (0.4%), respiratory failure (0.4%).

The posted serious adverse event figures list 1 affected participant among 263 at risk in the amoxicillin group and 3 among 263 at risk in the benzyl penicillin group. Other adverse events are listed as 0 among 263 at risk in each group. These are descriptive counts in the registry record and do not, by themselves, establish whether an event was caused by assigned treatment.

The registry lists congestive heart failure, hypovolemic shock, renal failure, and respiratory failure among the serious adverse event terms, each with a reported value of 0.4%. The record does not assign those terms to specific treatment groups in the posted term list, so they should not be attributed to one arm or the other from these summaries.

Deaths are listed as not available in the adverse-event group summaries. That is not the same as a report of zero deaths. The record does not provide enough information in this adverse-event summary to determine event timing, severity detail beyond the serious classification, relatedness assessments, or the completeness of adverse-event ascertainment. The counts are therefore best read as a compact safety description rather than a definitive comparison of treatment-related risk.

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

The results describe treatment-failure outcomes in this randomized trial of hospitalized children with severe pneumonia. The primary arm counts are close, and the recalculated risk difference is near zero. Yet the confidence interval spans values on both sides of no difference, so the data do not precisely identify a single direction or magnitude of the comparative effect.

The sponsor’s reported result is labeled as a non-inferiority or equivalence analysis. That label does not itself show that the required non-inferiority criterion was met. The margin and detailed decision rule are not reported in the registry record, so the posted summary is insufficient to verify a non-inferiority conclusion. A failure to find a statistically significant difference is also not the same as demonstrating equivalence.

The findings do not establish that either treatment works or does not work. They describe comparative outcomes in the enrolled trial population under the reported trial conditions. The open-label design, clinical elements in the failure definition, and unreported details about missing data and outcome assessment all affect how confidently the summaries can be interpreted.

Later outcomes add information about treatment failure and the day-14 death-or-readmission composite, but they differ from the primary endpoint in event definition and follow-up period. Separate results for listed readmission and death outcomes are not reported. The secondary comparisons therefore do not resolve the uncertainty around the primary comparison or substitute for a reported non-inferiority margin.

Finally, the statistical interpretation depends on both the estimate and its precision, along with the trial’s prespecified design criteria. The estimates are not forecasts for an individual child and do not establish what would occur in other hospitals or populations. The registry record supports a careful description of the posted group outcomes, but not a broader clinical recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority question cannot be answered by asking only whether a conventional difference test is statistically significant. A non-inferiority analysis needs a prespecified margin that defines how much worse the experimental treatment could be while still meeting the study’s criterion. The registry labels the sponsor result as non-inferiority or equivalence, but the margin and decision rule are not reported. That missing information prevents an independent check of the central inferential claim.

The record also makes the role of contrast direction visible. A risk difference changes sign when the arm order is reversed, so estimates need to be read with an explicit reference group. The recalculation and sponsor display use different numerical scales and signs, while the registry leaves the sponsor method unspecified. Clear reporting of the contrast, scale, and interval method is important for readers to reconcile analyses.

Precision matters alongside the point estimate. The primary interval includes values on both sides of no difference, and its interpretation depends on the acceptable boundary for non-inferiority. A point estimate near zero cannot replace that boundary or make the uncertainty disappear. The sample-size illustrations further show that the planning requirement depends on the effect size selected, but they do not recover the trial’s original design assumptions.

Finally, open-label outcome assessment, multiple secondary outcomes, and incompletely described missing-data handling are central to interpreting clinical trial summaries. The registry record presents a useful comparative dataset, but reporting the analysis plan, non-inferiority margin, multiplicity strategy, and follow-up handling would be necessary for a fuller assessment of the inferential claims.

19. Limitations

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

The open-label design is a trial-specific limitation. Participants and study personnel were not masked to assigned treatment, and the primary endpoint includes clinical judgments and treatment decisions, including a diagnosis requiring antibiotic revision. The registry does not report blinded outcome adjudication or other procedures intended to reduce the influence of knowledge of assignment.

The non-inferiority margin and its clinical or statistical justification are not reported. Without that threshold, the sponsor’s non-inferiority or equivalence classification cannot be independently evaluated from the posted interval. The sponsor’s statistical method is also not specified, which limits replication and reconciliation with the unadjusted recalculation.

The record does not describe the original sample-size assumptions, missing-data procedures, or sensitivity analyses. Although the primary population is named as intention to treat, this label does not explain how unavailable outcomes or deviations from assigned treatment were handled. Posted denominators differ across outcomes, and the reason for those differences is not reported.

Multiple secondary endpoints are listed, but the registry does not report a testing hierarchy or multiplicity adjustment. Results for readmission and death as separate outcomes are not reported, even though both are listed; the available composite does not distinguish its components. These gaps limit interpretation of later outcomes and the strength of any supportive claims.

The enrollment figure is 561, while the posted primary outcome arm denominators are 263 each. The registry does not explain the relationship between these entries. The trial’s reported dates and completed status do not fill in the missing details about recruitment, exclusions, or endpoint availability.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Amoxicillin Versus Benzyl Penicillin for Treatment of Children Hospitalised With Severe Pneumonia — NCT01399723.
• Registry record last updated 2015-02-13; status last verified 2015-01.
• Results first posted 2015-02-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, open-label, parallel-group phase 3 trial comparing amoxicillin with benzyl penicillin for severe pneumonia among hospitalized children. Enrollment is listed as 561, with study start in 2011-09 and primary completion in 2013-09.

The primary outcome is treatment failure at 48 hours in an intention-to-treat analysis. Posted results show 20 events among 263 participants assigned to amoxicillin and 21 among 263 assigned to penicillin. The sponsor reports a risk difference of -0.4 with a 95% confidence interval from -5.0 to 4.2 and classifies the analysis as non-inferiority or equivalence. The margin and detailed method are not reported in the registry record.

Posted secondary results include treatment failure by discharge or day 5 and a day-14 death-or-readmission composite. Their definitions and follow-up differ from the primary endpoint. The registry also lists adverse-event counts, but the summaries do not establish causation or provide complete detail about event attribution. Interpretation is limited by unreported analysis specifications, missing-data handling, and multiplicity procedures.