Procalcitonin-Guided Decision Making to Shorten Antibiotic Therapy in Suspected Neonatal Early-Onset Sepsis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Procalcitonin-Guided Decision Making to Shorten Antibiotic Therapy in Suspected Neonatal Early-Onset Sepsis (NCT00926497), a randomized na study. The primary outcome is Antibiotic Treatment for More Than 72 Hours.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group intervention trial with no masking. Enrollment was 121, and the trial status is completed. The procalcitonin-guided group included 60 infants and the standard group included 61. The record lists the study phase as not applicable.

In the intervention group, decisions to stop antibiotic therapy were guided by procalcitonin measurements: discontinuation was permitted after two consecutive values below predefined age-adjusted cut-off values. The attending physician retained discretion to prolong treatment even when the procalcitonin criteria were met. The comparator was standard treatment based on conventional laboratory parameters. The registry record does not report more detail about the timing or frequency of measurements, treatment protocols beyond these descriptions, or how physicians applied their discretion.

The primary endpoint was the number of infants treated with antibiotics for more than 72 hours, assessed over a timeframe of 1 month. This binary endpoint records whether each infant crossed the stated duration threshold; it does not provide the actual treatment duration for each infant. The registry record reports 33 infants in the procalcitonin group and 55 in the standard group meeting the endpoint. It does not describe the trial's original sample-size assumptions or provide detailed eligibility criteria, site information, or the complete statistical analysis plan.

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 Antibiotic Treatment for More Than 72 Hours, measured over 1 month.

The primary endpoint counts infants who received antibiotics for more than 72 hours. It is recorded as a participant count, so each infant is classified according to whether the duration crossed that threshold. The stated timeframe is 1 month. The registry describes this measure as the efficacy of the study intervention.

A threshold-based endpoint can make a treatment-duration question straightforward to interpret: it indicates how many participants in each group received antibiotics beyond the specified duration. It does not show the full distribution of treatment durations, distinguish small from large extensions beyond the threshold, or explain the clinical reasons for continuing therapy. Nor does the endpoint alone assess other outcomes, such as the course of infection or longer-term health.

In the procalcitonin group, 33 of 60 infants met the endpoint; in the standard group, 55 of 61 did. These counts describe the posted primary result. The analysis compares the chance of meeting this binary endpoint between randomized groups, but the registry record does not provide an endpoint definition for a broader clinical benefit or harm composite. The endpoint should therefore be read specifically as antibiotic treatment beyond 72 hours, not as a complete measure of treatment success or safety.

7. Results Posted in the Registry

• Procalcitonin-group: 55.0% (33/60) versus 90.2% (55/61) on control; risk difference -35.2 percentage points (95% CI -49.8 to -20.5), risk ratio 0.61 (0.48–0.78); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the binary endpoint count?

A binary endpoint places each participant into one of two categories: the event occurred or it did not. In this trial, the event was antibiotic treatment for more than 72 hours. The recorded counts were 33 in the procalcitonin-guided group and 55 in the standard group. The corresponding group sizes were 60 and 61. This form of data is useful for comparing the frequency of an event, but it discards detail about how long treatment continued for each participant.

For a binary endpoint, common effect measures include a risk difference, risk ratio, and odds ratio. They express the group contrast in different ways. A risk difference describes the difference between event proportions; a risk ratio compares those proportions as a ratio; an odds ratio compares event odds. These measures are not interchangeable, and their interpretation depends on which group is used as the reference and how the contrast is ordered. The registry record includes a recalculated risk-difference comparison and ratio measures, but the principal interpretation focuses on the count outcome and the reported test.

What does the Fisher Exact test assess?

The sponsor's posted analysis is identified as a Fisher Exact test. In general, this test evaluates whether the observed allocation of binary outcomes across groups would be unusual under a null hypothesis of no association between group and outcome. It is a test of compatibility with that null model, not a measure of the size or clinical importance of a difference. A p-value is not the probability that the null hypothesis is true, nor does it quantify the chance that the observed pattern will recur.

The registry reports p = 0.002 for the sponsor's Fisher Exact analysis. A separate simple unadjusted re-calculation from the posted summary counts gives p < 0.001. Because the two values are reported from distinct analyses, they should not be presented as if they were one identical calculation. The registry record does not provide further details that explain the difference. The interpretation of the sponsor's analysis should remain anchored to the test the sponsor reported.

How should an effect estimate and interval be read?

An effect estimate summarizes the observed group contrast, while a confidence interval describes the uncertainty associated with that estimate under the statistical method used. For the re-calculated risk difference, the interval endpoints lie on the same side of zero. In general, an interval that excludes zero for a difference is inconsistent with a zero contrast at the corresponding confidence level, subject to the assumptions of the calculation. It does not remove uncertainty, prove a particular mechanism, or show that the estimate will be identical in other populations.

Intervals and p-values answer related but different questions. The p-value summarizes how compatible the data are with a specified null model. The interval gives a range of effect values compatible with the data and method at a stated confidence level. Neither should be interpreted in isolation from the endpoint, design, and limitations. The registry lists a 95% confidence level for the sponsor analysis, but its analysis estimate and interval endpoints are not reported.

Why does randomization matter, and what does it not resolve?

Random allocation is intended to make comparison groups similar on average with respect to measured and unmeasured factors at assignment. This supports interpreting between-group differences as associated with assignment to the intervention rather than as a simple comparison of pre-existing groups. Randomization does not ensure that every feature is balanced in a particular trial, and it does not resolve bias introduced by outcome measurement, deviations from assigned treatment, missing data, or analysis choices.

The trial was unmasked. That means the registry does not describe masking of participants or clinical staff, and the attending physician's discretion to prolong antibiotics is part of the intervention description. In general, knowledge of group assignment can influence decisions or measurement, depending on the outcome. The primary endpoint is a duration threshold, and the record does not report further procedures for keeping its assessment independent of treatment decisions.

What is not reported about the analysis?

The registry record does not report the original sample-size justification, a prespecified analysis plan, interim analyses, covariate adjustment, missing-data methods, or a detailed definition of the analysis population. These absences matter because analytic decisions can affect precision and interpretation. They should not be filled in by assuming customary procedures. The reported analyses and counts can be described, while the unreported methods remain uncertain.

The registry lists two outcome measures and three analyses, but no secondary results are posted. It is not reported whether any multiplicity adjustment was planned or applied. Multiple comparisons can increase the chance of at least one apparently notable result if tests are interpreted without accounting for their number. Without a reported plan and full results, it is not possible to assess how that issue was handled. Likewise, no details about protocol deviations or missing endpoint observations are reported.

10. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated group contrast. A confidence interval gives a range of values compatible with the observed data and the method used, at a stated confidence level. It should be read alongside the event counts and the endpoint definition, rather than as a guarantee that the true effect lies within a fixed range or that future results must fall inside it.

The re-calculated risk-difference interval has both endpoints below zero under the stated direction of comparison. Thus, the interval does not include a zero difference. This indicates that the re-calculated data are not especially compatible with a zero contrast under the interval's assumptions, but it does not establish the precision of every other possible outcome measure. The risk-difference estimate and its interval are re-calculations from the posted summary counts, not an interval reported by the sponsor.

The registry identifies a 95% confidence level for the sponsor's Fisher Exact analysis, but it does not report the sponsor's estimate or interval endpoints. Consequently, the sponsor's interval width cannot be assessed from the registry record. The sponsor's reported p-value and the re-calculated interval are related evidence about the primary comparison, but they are not the same statistic.

Even when an interval excludes zero, its width matters: a narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size of the contrast. The available group counts and re-calculated interval support a direction for this endpoint, but the open-label design, unreported analysis details, and absence of posted secondary results limit how broadly that precision can be interpreted. Precision for safety outcomes is especially difficult to assess because adverse-event denominators are not reported.

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 are illustrations based on the observed effect, not the trial's original design assumptions; those original assumptions are not reported in the registry record. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers planning for 100%, 75%, or 50% of the observed effect.

The 80% power column gives the planned number of participants per arm for a design intended to have an 80% probability of detecting the chosen effect under the stated assumptions, if that effect were the true one. The 90% power column gives the corresponding planning number for a design intended to have a 90% probability. These are design targets, not guarantees about what a future study will find. Planning for 100% of the observed effect gives 25 participants per arm for 80% power and 32 for 90% power. Planning for 75% gives 39 and 52, respectively. Planning for 50% gives 76 and 101, respectively.

Smaller effects require more participants to detect under otherwise unchanged assumptions, because a smaller difference is harder to distinguish from random variation. The illustration uses an effect observed in this trial, so it is sensitive to the uncertainty and potential overestimation associated with an observed effect. This is not observed power; it is a set of planning illustrations under stated assumptions.

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 = 0.902; treatment proportion p₁ = 0.550; average p̄ = 0.726.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6309 = 1.2365.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5798 = 0.4880.
4. n = (1.2365 + 0.4880)² / (-0.3516)² = 24.1, rounded up to 25 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 <- 0.901639344262295                          # control proportion
p1 <- 0.55                          # 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(926497)
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 = 25 (80% power), 32 (90% power)
 75% of observed effect: n per arm = 39 (80% power), 52 (90% power)
 50% of observed effect: n per arm = 76 (80% power), 101 (90% power)
power.prop.test: 24.1 
Simulated power at n = 25 per arm: 0.842 (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 reports the sponsor's primary comparison as a Fisher Exact test with p = 0.002. Separately, a simple unadjusted re-calculation from the posted group counts gives p < 0.001. The registry record does not provide enough detail to reconcile these values or to establish that the analyses used identical procedures. The re-calculation should therefore be understood as a check based on the posted summary counts, not as a replacement for the sponsor's analysis.

The two reported p-values lead to the same broad statistical reading: each is evidence against equal event proportions under the respective test. Their numerical difference does not change the fact that the event counts were 33 of 60 in the procalcitonin group and 55 of 61 in the standard group. Neither p-value alone describes the size or practical importance of the contrast, and neither extends the result to unreported outcomes.

The record does not provide the sponsor's effect estimate, confidence interval endpoints, or a detailed analysis plan. The re-calculated effect measures are thus supplementary descriptions derived from the posted counts. Interpretation should preserve the distinction between the sponsor-reported test and the unadjusted re-calculation rather than suggesting that one reproduces the other.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists two outcome measures and three analyses, while no secondary results are posted. It does not report whether the primary endpoint was designated in a prespecified statistical analysis plan, how the remaining outcome measure relates to the primary question, or whether all planned analyses are represented. The absence of these details prevents a full assessment of selective reporting.

Multiplicity arises when several outcomes, comparisons, or analyses are tested. In general, performing multiple tests without an appropriate plan can raise the chance of at least one result appearing statistically notable by chance. The registry record does not report whether any adjustment for multiple testing was planned or used, so it is not possible to assess that issue for this trial. The existence of multiple analyses alone does not establish that the sponsor's primary result was selected after examining the data.

Missing-data handling and analysis populations are also not reported. The record does not state whether every randomized infant had an observed primary endpoint, how any missing endpoint information was handled, or whether the analyses followed intention-to-treat, per-protocol, or another population definition. The posted group sizes and event counts can be described, but they do not by themselves explain exclusions, protocol deviations, or missing observations.

For adverse events, the registry reports no serious adverse events in either group, one other adverse event in the procalcitonin group, and none in the standard group. The numbers at risk for these adverse-event summaries are not reported, and deaths are not reported. Without denominators or a fuller safety analysis, these entries cannot establish comparative event rates. The registry record also does not report imputation methods, sensitivity analyses, interim analyses, or further safeguards against missing-data bias.

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

The primary result means that fewer infants in the procalcitonin-guided group were recorded as receiving antibiotics for more than 72 hours than in the standard group: 33 of 60 compared with 55 of 61. This is a result for a specific duration threshold during the stated timeframe of 1 month. It does not describe the complete distribution of antibiotic duration or the reasons clinicians chose to continue treatment.

The randomized comparison and the reported statistical tests provide evidence of a difference in this recorded endpoint between the assigned groups. That finding is not, by itself, a full assessment of clinical benefit, safety, or patient-important outcomes. The registry record does not post secondary outcome results, and the available adverse-event entries do not include denominators. It therefore cannot support conclusions about outcomes that are not reported.

The intervention included physician discretion to prolong therapy even after the procalcitonin criteria were met. The observed group contrast reflects the intervention as described in the trial, including that discretion, rather than an automatic stopping rule applied in every case. The record does not report how often the criteria were fulfilled or how often treatment was continued despite them.

The open-label design and unreported details about missing data, analysis populations, and the statistical plan constrain interpretation. The reported statistical evidence should not be turned into a claim that an approach will have the same effect in every clinical setting. Nor does a statistically notable comparison establish that the difference is large enough to matter clinically. The result is best understood narrowly as a difference in the recorded count of infants treated beyond the specified duration threshold.

16. Why This Trial Matters Statistically

This trial presents a clear statistical contrast between a binary treatment-duration endpoint and a randomized group assignment. The endpoint is easy to state—antibiotic treatment for more than 72 hours—but its simplicity also marks its limits. It captures whether an infant crossed a threshold, not how much longer treatment continued or why.

The trial also illustrates the importance of separating the sponsor's analysis from an unadjusted re-calculation. The registry reports a Fisher Exact p-value of 0.002, while a re-calculation from the posted counts gives p < 0.001. These are distinct statistical results, and their reporting should not be collapsed into a single figure. The counts remain essential context for understanding what each test is comparing.

Randomization strengthens the group comparison, while the unmasked design and clinician discretion show why implementation details matter. A decision-guided intervention can include judgment at the point of care; the resulting endpoint reflects both the decision rule and the allowance for physicians to extend treatment.

Finally, the record highlights a recurring interpretive challenge in trial registries: a primary result can be available even when secondary outcomes, analysis populations, missing-data procedures, and original design assumptions are not. Statistical significance alone cannot fill those gaps. Careful interpretation depends on defining exactly what was counted, distinguishing reported from recalculated analyses, and keeping conclusions within the information the record contains.

17. 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 trial was unmasked, and the attending physician could prolong antibiotics despite meeting the procalcitonin stopping criteria. The registry record does not report how frequently that discretion was used, or whether endpoint assessment was independently reviewed. This makes it difficult to distinguish the contribution of the biomarker-guided rule from the contribution of clinical judgment in individual decisions.

The endpoint is a binary threshold for treatment beyond 72 hours. The registry does not report the actual durations, the reasons for treatment extension, or results for other clinical outcomes. The primary endpoint therefore offers a limited view of treatment exposure and cannot by itself characterize the overall clinical course.

The registry record does not report detailed eligibility criteria, baseline characteristics, missing-data procedures, analysis populations, protocol deviations, or the original sample-size justification. It also does not report the complete statistical plan, any interim analyses, or whether multiplicity was considered. These omissions limit assessment of representativeness, analytic choices, and the robustness of the posted result.

The sponsor's reported p-value differs from the simple unadjusted re-calculation based on posted counts, and the record does not supply detail that reconciles them. Safety entries have no reported at-risk denominators, and deaths are not reported. No secondary outcome results are posted. These limitations call for a narrow reading of the primary comparison rather than conclusions about unreported outcomes or settings.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Procalcitonin-Guided Decision Making to Shorten Antibiotic Therapy in Suspected Neonatal Early-Onset Sepsis — NCT00926497.
• Registry record last updated 2009-06-23; status last verified 2009-05.
• Results first posted 2009-06-23.
• 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.

21. Record Summary

NCT00926497 is a completed randomized, parallel-group trial with no masking. It enrolled 121 participants and compared procalcitonin-guided decisions with standard treatment based on conventional laboratory parameters for suspected neonatal early-onset sepsis.

The primary endpoint counted infants treated with antibiotics for more than 72 hours over a timeframe of 1 month. The registry reports 33 of 60 infants meeting the endpoint in the procalcitonin group and 55 of 61 in the standard group. The sponsor's analysis was a Fisher Exact test with p = 0.002; an unadjusted re-calculation from the posted counts gives p < 0.001.

The registry record does not report secondary outcome results, detailed analysis-population or missing-data methods, or the original design assumptions. Adverse-event denominators and deaths are not reported. The findings should be interpreted as a comparison of the specified antibiotic-duration endpoint, not as a complete account of clinical outcomes.