Phase 4 Comparative Trial of Benzathine Penicillin G for Treatment of Early Syphilis in Subjects With or Without HIV Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 4 Comparative Trial of Benzathine Penicillin G for Treatment of Early Syphilis in Subjects With or Without HIV Infection (NCT03637660), a randomized phase 4 study. The primary outcome is The Number of Participants With a Serological Response by Month 6..

2. Clinical Question

The trial compared two schedules of benzathine penicillin G (BPG) for adults with untreated early syphilis: a single intramuscular dose of 2.4 million units and 2.4 million units administered weekly for three successive weeks. It included subjects with or without HIV infection. The central question was whether the serological response by Month 6 differed between the schedules, using a response definition based on RPR results.

The comparison concerns a laboratory-defined response over the period from Day 1 to Day 180. It does not, by itself, answer every question about symptoms, longer-term outcomes, adherence, or safety. The registry also includes a Month 12 serological response outcome and other secondary measures, but those address different aspects of the trial and should be interpreted separately from the primary comparison.

3. Trial Design

The registry describes this as a Phase 4, randomized, open-label, multicenter, parallel-group trial. Participants were assigned to one of the two BPG schedules. Masking was none, so the study was open-label. The registry record lists Syphilis as the condition and the National Institute of Allergy and Infectious Diseases (NIAID) as the sponsor.

The registry lists actual enrollment as 249. The brief summary describes a planned enrollment of 560 adults, with the aim of achieving 420 evaluable subjects. It also describes a planned study at 9 US sites, a 48-month study duration, and participant participation lasting 12 months. Those figures are planning descriptions; the record separately lists the trial status as completed, with a start date of 2018-10-31 and primary completion date of 2022-09-07.

The treatment-arm descriptions specify planned assignments of n=280 to each schedule. For the primary outcome, the posted arm denominators are 124 for the one-dose group and 125 for the three-dose group. The registry identifies the primary analysis population as the intention-to-treat population: all randomized subjects, irrespective of whether they received treatment or followed administration procedures or schedules.

The primary outcome timeframe is Day 1 to Day 180. Secondary outcomes include a Month 12 serological response, receipt of assigned doses within visit windows, and reports of Jarisch-Herxheimer reaction manifestations, along with baseline descriptive measures. The registry record does not report the original sample-size justification, randomization procedure details, or a fuller 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

Analysis population for the primary outcome, as defined in the registry: The ITT Population includes all randomized subjects, regardless of whether they received study treatment or were compliant with the administration procedures or schedule.

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 The Number of Participants With a Serological Response by Month 6., measured over Day 1 to Day 180.

The primary endpoint counts participants with a serological response by Month 6. It uses RPR results available before the end of the Month 6 visit window, including scheduled visits up to and including Month 6, early termination visits, and unscheduled visits that occurred before the window ended.

A participant met the response definition if either of two conditions was satisfied: an RPR titer decline of 4-fold or greater from baseline at an eligible visit, or an RPR-negative result at an eligible visit. The latter is described as seroreversion. The endpoint is therefore binary at the participant level: each participant is counted as having or not having a response according to the stated definition.

Serological response is used because it captures a change in a laboratory marker after treatment over a specified follow-up period. A count of responders can be compared between randomized groups, while retaining the clinical meaning of the registry's response definition. It is not a direct measure of every aspect of the disease or of a participant's experience. The endpoint's interpretation also depends on which RPR observations were available and how missing observations were handled; those details are not reported in the registry record.

7. Results Posted in the Registry

• Three Doses BPG 2.4 MU: 69.6% (87/125) versus 75.8% (94/124) on control; risk difference -6.2 percentage points (95% CI -17.2 to 4.8), risk ratio 0.92 (0.79–1.07); unadjusted two-proportion z-test p = 0.272.

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.

The Number of Participants Who Receive All Assigned Doses Within the Assigned Visit Windows

• 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:
  • Three Doses BPG 2.4 MU: 77.6% (97/125) versus 100.0% (124/124) on control; risk difference -22.4 percentage points (95% CI -29.7 to -15.1), risk ratio 0.78 (0.71–0.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Three Doses BPG 2.4 MU than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The Number of Participants Who Report Jarisch-Herxheimer Reaction Manifestations

• 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:
  • Three Doses BPG 2.4 MU: 25.6% (32/125) versus 21.8% (27/124) on control; risk difference 3.8 percentage points (95% CI -6.7 to 14.4), risk ratio 1.18 (0.75–1.84); unadjusted two-proportion z-test p = 0.478.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Three Doses BPG 2.4 MU and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Serological Response (Defined as Either a 4-fold or Greater Decline in Rapid Plasma Regain (RPR) Titer Compared to Baseline or Being Rapid Plasma Regain -Negative [Seroreversion]) by Month 12.

• 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:
  • Three Doses BPG 2.4 MU: 72.8% (91/125) versus 78.2% (97/124) on control; risk difference -5.4 percentage points (95% CI -16.1 to 5.2), risk ratio 0.93 (0.81–1.07); unadjusted two-proportion z-test p = 0.320.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Three Doses BPG 2.4 MU and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several different topics: adherence to assigned dosing windows, Jarisch-Herxheimer reaction manifestations, Month 12 serological response, and descriptive characteristics collected at baseline. These outcomes complement the Month 6 primary endpoint by addressing treatment delivery, a reported reaction, later serological response, and participant characteristics. They do not all measure the same underlying question, and their results should not be treated as interchangeable evidence about the primary outcome.

The posted Month 12 response comparison has a direction similar to the Month 6 recalculation, while the dose-window outcome reflects completion of the assigned schedules and the Jarisch-Herxheimer outcome concerns manifestations during the early period specified in the registry. These distinct outcomes may help describe the trial experience, but they do not independently settle the primary non-inferiority question. The sponsor's own reported Month 12 analysis is also a non-inferiority analysis, separate from the recalculated comparison.

Secondary outcomes generally carry less inferential weight when many outcomes are examined without a reported multiplicity strategy. The registry lists 27 outcome measures and reports 7 analyses, with 26 secondary outcomes posted. A notable result among many tests can arise by chance, and the registry record does not report whether adjustment, outcome hierarchy, or a prespecified testing sequence was used. For that reason, secondary findings are best viewed as descriptive or supportive unless the analysis plan clarifies their confirmatory status. No single secondary result should be used to override the primary analysis or to imply a broader treatment conclusion than the outcome measures support.

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

• Categorical Descriptive Statistics of Sexual History at Baseline Collected Via a Study-specific Questionnaire
• Continuous Descriptive Statistics of Sexual History at Baseline Collected Via a Study-specific Questionnaire
• Categorical Descriptive Statistics of Socio-epidemiologic Characteristics at Baseline Collected Via a Study-specific Questionnaire
• Continuous Descriptive Statistics of Socio-epidemiologic Characterictics at Baseline Collected Via a Study-specific Questionnaire
• Categorical Descriptive Statistics of Participant Baseline Demographics Collected Via a Study-specific Questionnaire
• Continuous Descriptive Statistics of Participant Baseline Demographics Collected Via a Study-specific Questionnaire
• The Number of Participants Who Receive All Assigned Doses Within the Assigned Visit Windows
• The Number of Participants Who Report Jarisch-Herxheimer Reaction Manifestations

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either met the serological response definition by Month 6 or did not. For a binary outcome, each group's response proportion is the number of participants with the outcome divided by the number assessed in that group. A comparison can be expressed as a risk difference, which subtracts the reference group's proportion from the other group's proportion. Here, the recalculated contrast is defined for three doses relative to one dose. Its sign therefore indicates the direction of the observed difference, and zero would correspond to equal proportions.

The recalculated estimates use the posted arm counts and denominators without adjustment. This is a straightforward summary, but it does not account for any covariates, stratification, or other features that might have been used in the sponsor's analysis. The registry's sponsor analysis uses the Farrington-Manning method and is explicitly labelled non-inferiority. That method is designed for a non-inferiority framework rather than simply testing whether two proportions differ. The method evaluates the estimate in relation to a margin that represents the largest acceptable loss. The margin is not reported in the registry record, so the non-inferiority criterion cannot be reconstructed from the posted information alone.

A p-value summarizes how compatible the data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted p-value for the recalculated Month 6 comparison addresses a difference-testing framework. The sponsor's p-value belongs to the reported non-inferiority analysis. These values should not be compared as if they tested the same null hypothesis.

A confidence interval describes a range of estimates compatible with the data and the method's assumptions. For a risk difference, an interval crossing zero allows no difference as one possibility. For a non-inferiority analysis, interpretation also depends on the direction and location of the interval relative to the prespecified margin. Since that margin is not reported, the sponsor's classification can be quoted, but its threshold cannot be independently checked from the registry record.

Randomization is intended to make treatment groups comparable on average, including for factors that were not measured. It does not guarantee identical groups in a particular trial. An open-label design means treatment assignment was not masked. The primary endpoint is based on laboratory results, but the registry record does not report whether laboratory assessment was blinded or describe procedures to limit assessment bias. The record also does not provide details of allocation concealment, randomization strata, or adjustment covariates.

The intention-to-treat population is described as all randomized subjects, regardless of treatment receipt or compliance. This retains participants in their assigned groups and preserves the central benefit of randomization. The endpoint denominators posted for the primary outcome are 124 and 125; the registry record does not explain the relationship of those denominators to all randomized subjects or how unavailable RPR results were treated. The specific missing-data method, if any, is not reported.

Multiplicity arises when several outcomes or statistical tests are examined. The registry lists 27 outcome measures and reports 7 analyses; 26 secondary outcomes are posted. Testing many outcomes can increase the chance of at least one apparently notable result by chance. Adjustments or a prespecified hierarchy can address that concern, but such procedures are not reported in the registry record. Therefore, secondary findings should generally be treated as supportive or exploratory unless their testing plan is available.

In general, over-dispersion is relevant to count outcomes when variation exceeds what a simple count model assumes. The posted primary result is a participant count for a binary response, not a rate with a reported dispersion estimate, so no over-dispersion adjustment is indicated in the posted primary analysis. More broadly, statistical methods should match the outcome's scale and the trial question. The registry record does not report additional modeling details, sensitivity analyses, or interim analyses, so none can be assumed.

The registry's own reported analysis and the unadjusted recalculation serve different roles. The reported Farrington-Manning result is the sponsor's non-inferiority analysis. Recalculated risk differences and intervals are simple summaries based on posted counts and do not constitute a substitute analysis plan. Where the registry flags a discrepancy, the sponsor analysis takes precedence for describing the trial's own inferential result, while the recalculation can help readers understand the observed contrast and its statistical precision.

11. Confidence Intervals and Precision

The recalculated Month 6 risk difference for three doses relative to one dose is -0.062, with an interval from -0.172 to 0.048. The interval spans zero and includes differences in either direction. It therefore does not pin down a single precise contrast between schedules. The registry record does not state the confidence level for this recalculated interval, so it should not be labelled with a confidence percentage that is not reported.

The sponsor's Month 6 analysis reports a 90% confidence interval from -0.15 to 0.03 around a difference of -0.06. Its interpretation is tied to non-inferiority, not simply to whether the interval crosses zero. Without the non-inferiority margin, the reported conclusion cannot be independently assessed against its decision threshold. The interval itself communicates uncertainty in the estimated difference, but it does not show the margin used by the sponsor.

For the Month 12 response, the recalculated interval runs from -0.161 to 0.052 around a risk difference of -0.054. This also spans zero. As with the primary recalculation, the confidence level is not reported in the registry record. The sponsor reports a 90% interval from -0.14 to 0.04 for its Month 12 non-inferiority analysis.

Intervals are more informative than a binary significant/not-significant label because they show the range of effect sizes compatible with the data under the method used. A wide interval indicates limited precision; a narrow interval indicates greater precision. Even when an interval includes zero, it may still include differences that could matter. The posted intervals therefore support cautious interpretation rather than a claim of exact equality. Their precision reflects the available participants and outcome information, while the trial's original precision target and assumptions are not reported in the registry record.

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 values are participants per arm for 80% power and participants per arm for 90% power. They are not total events. The calculation assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. These are planning assumptions for the illustration, not the trial's own original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column gives the corresponding estimate for a 90% chance. Higher target power generally requires a larger planned sample when other assumptions are unchanged. These figures are planning illustrations, not observed power.

The entries are shown for planning at 100%, 75%, and 50% of the observed effect. As the effect to be detected becomes smaller, more participants are needed to distinguish it from random variation with the same target power. For the primary response comparison, the listed estimates rise from 808 participants per arm at 100% of the observed effect to 1,411 at 75% and 3,116 at 50% for 80% power. For 90% power, the corresponding listed values are 1,081, 1,888, and 4,170 per arm. These are not estimates of the trial's actual enrollment requirement or evidence about its achieved power. The registry record's original sample-size justification is not reported.

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 = 0.758; treatment proportion p₁ = 0.696; average p̄ = 0.727.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6300 = 1.2348.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6285 = 0.5289.
4. n = (1.2348 + 0.5289)² / (-0.0621)² = 807.6, rounded up to 808 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 <- 0.758064516129032                          # control proportion
p1 <- 0.696                          # 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(3637660)
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 = 808 (80% power), 1,081 (90% power)
 75% of observed effect: n per arm = 1,411 (80% power), 1,888 (90% power)
 50% of observed effect: n per arm = 3,116 (80% power), 4,170 (90% power)
power.prop.test: 807.6 
Simulated power at n = 808 per arm: 0.798 (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 reports the primary comparison using the Farrington-Manning method, with a difference of -0.06, a 90% confidence interval from -0.15 to 0.03, and p = 0.002. The analysis is classified as non-inferiority. The sponsor also reports a Month 12 non-inferiority analysis with a difference of -0.05, a 90% confidence interval from -0.14 to 0.04, and p = 0.002.

The recalculated primary comparison is a simple unadjusted risk difference of -0.062 with an interval from -0.172 to 0.048 and p = 0.272. It is not the same analysis: it uses a direct difference-testing calculation from the posted counts, whereas the sponsor's analysis addresses non-inferiority. The registry record flags a discrepancy, so the sponsor's own analysis takes precedence when describing the trial's inferential result.

The non-inferiority margin and full analysis details are not reported in the registry record. The sponsor's stated non-inferiority result can therefore be described as reported, but the threshold supporting that conclusion cannot be independently checked from the record. The recalculation is useful as a transparent description of the raw group contrast, not as a replacement for the sponsor's analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies the intention-to-treat population for the primary outcome as all randomized subjects, regardless of treatment receipt or compliance with administration procedures or schedules. This definition is important because it retains participants in their assigned groups for the main comparison. The posted primary outcome denominators are 124 in the one-dose group and 125 in the three-dose group, but the registry record does not explain whether every randomized subject had an evaluable Month 6 RPR result or how participants without an available result were classified.

The missing-data approach is not reported in the registry record. It is therefore not possible to determine whether missing RPR results were excluded, imputed, handled as non-response, or addressed through sensitivity analyses. The record also does not report additional analysis populations, such as a per-protocol population, or explain how any such population might relate to the non-inferiority analysis. These omissions matter because missing observations and departures from assigned dosing can affect estimates, and non-inferiority conclusions can be sensitive to analysis choices.

The registry lists 27 outcome measures, 26 posted secondary outcomes, and 7 reported analyses. It does not report a multiplicity adjustment, a confirmatory hierarchy for outcomes, or a complete prespecified sequence of tests. Without that information, isolated secondary p-values should be interpreted cautiously. Interim analyses and any associated stopping rules are also not reported in the registry record. These details are relevant to evaluating the full inferential plan, but their absence does not change the posted outcome counts or the sponsor analysis as reported.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: proctocolitis (0.8%), substance induced psychotic disorder (0.8%), right sided facial weakness (0.8%).

The adverse-event information lists serious adverse events affecting 1 participant in the one-dose group, among 124 at risk, and 2 participants in the three-dose group, among 125 at risk. Deaths are listed as 0 in both groups. The registry also names Proctocolitis, Substance Induced Psychotic Disorder, and Right Sided Facial Weakness among the top serious terms, each reported as 0.8%.

These figures describe the serious adverse-event information recorded in the registry; they do not establish that treatment caused an event. The counts are small, and the registry record does not provide event timing, attribution, severity details beyond the serious classification, or additional context needed to assess causation. The listed terms and percentages should be read as reported categories, not as a complete account of every safety outcome. The separate count of participants reporting Jarisch-Herxheimer reaction manifestations is a secondary outcome and is not the same measure as the serious adverse-event summary.

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

The posted Month 6 counts show that serological responses were recorded in both groups. The recalculated difference is modest in direction and has an interval that includes zero, indicating uncertainty about the exact contrast. The sponsor's own analysis reports non-inferiority using the Farrington-Manning method. Because the registry record does not report the margin, readers cannot independently verify the threshold used for that conclusion from the posted information alone.

The result does not establish that the schedules are identical. A non-inferiority finding is not a demonstration of equivalence, and failure of an unadjusted difference test to show a clear difference is not proof of no difference. The results also do not show that either schedule is better. The interpretation is limited to the endpoint definition, follow-up period, analysis population, and statistical procedures described in the registry.

The primary endpoint is a laboratory-based response through Month 6, defined using RPR decline or seroreversion. It does not encompass every clinical outcome, participant preference, longer-term result, or aspect of treatment delivery. The registry posts a Month 12 response measure and selected secondary outcomes, but those measures have distinct purposes and do not erase uncertainty in the primary comparison.

These findings are statistical descriptions of the trial record, not medical advice. The registry does not report enough detail to assess the original sample-size justification, missing-data procedures, multiplicity handling, or all assumptions behind the sponsor's non-inferiority analysis. Those gaps should temper how broadly the reported conclusion is generalized.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical question matters as much as the observed counts. A difference test asks whether the data provide evidence against equal response proportions. A non-inferiority test asks whether the data rule out a loss larger than a prespecified margin. The sponsor reports the latter framework, while the simple recalculation describes an unadjusted difference. Treating those analyses as if they answered the same question would misstate the evidence.

It also demonstrates the importance of a clearly reported non-inferiority margin. The sponsor's conclusion is identified as non-inferiority, but the margin is not reported in the registry record. Without it, the decision threshold cannot be independently evaluated. Reporting the estimate and confidence interval is useful, but readers also need the criterion against which those values were judged.

The trial further highlights the distinction between observed enrollment and planned sample size. The registry reports enrollment of 249, while the brief summary describes a plan to enroll 560 adults and achieve 420 evaluable subjects. Planning illustrations based on the observed effect can help explain how sample needs change with the target effect and power, but they do not explain the trial's original design decisions.

Finally, the combination of a primary endpoint, numerous secondary measures, and unreported multiplicity procedures makes careful prioritization important. The primary result, sponsor analysis, secondary outcomes, and safety counts each answer different questions. Keeping these roles distinct supports a more accurate reading of the statistical evidence.

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.

Several trial-specific reporting gaps limit independent assessment. The non-inferiority margin is not reported, even though the sponsor analysis is classified as non-inferiority. The registry record also does not report the original sample-size justification, the full statistical analysis plan, randomization implementation details, or any interim analyses. These details would help readers understand the planned inference and its assumptions.

The record describes an intention-to-treat primary population, but it does not report how missing Month 6 RPR results were handled, whether other analysis populations were used, or how departures from assigned dosing were treated in the sponsor's analysis. The posted arm denominators are smaller than the planned arm assignments described in the intervention information, but the record does not explain the participant flow that produced the outcome denominators. The relationship between actual enrollment and the planned evaluable target is likewise not explained.

The trial was open-label, and the registry record does not state whether outcome assessment or laboratory assessment was blinded. The record also does not provide enough detail to evaluate potential sources of bias beyond the stated design features. The reported adverse-event information is limited to selected counts and terms, without event-level timing or attribution details.

Finally, multiple outcomes are listed, while multiplicity handling is not reported. The recalculated comparisons are unadjusted summaries and do not reproduce the sponsor's non-inferiority method. These limitations do not invalidate the posted results, but they restrict how completely the statistical analysis and broader implications can be assessed from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 4 Comparative Trial of Benzathine Penicillin G for Treatment of Early Syphilis in Subjects With or Without HIV Infection — NCT03637660.
• Registry record last updated 2025-01-14; status last verified 2019-09-19.
• Results first posted 2023-12-26.
• 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.

23. Record Summary

NCT03637660 is a completed Phase 4, randomized, open-label, parallel-group comparison of one intramuscular dose of BPG 2.4 million units with three successive weekly doses for early syphilis in subjects with or without HIV infection. Actual enrollment is listed as 249. The primary outcome counted participants with a serological response by Month 6, defined by an RPR decline of 4-fold or greater or an RPR-negative result within the specified visit window.

The sponsor reports a Farrington-Manning non-inferiority analysis for the primary outcome. An unadjusted recalculation gives a risk difference of -0.062, with an interval from -0.172 to 0.048 and p = 0.272; the registry flags a discrepancy, so the sponsor's analysis takes precedence as the trial's reported inferential result. The non-inferiority margin, missing-data handling, multiplicity procedures, and original sample-size justification are not reported in the registry record.