Comparison of Doxycycline and Cefuroxime Axetil for Treatment of Erythema Migrans: Clinical and Microbiological Outcome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Doxycycline and Cefuroxime Axetil for Treatment of Erythema Migrans: Clinical and Microbiological Outcome (NCT01518192), a randomized phase 4 study. The primary outcome is Objective Lyme Disease Manifestations and Post-Lyme Disease Symptoms at 14 Days.

2. Clinical Question

3. Trial Design

The registry describes NCT01518192 as a randomized, parallel-group, open-label Phase 4 trial. Its listed enrollment is 544, and its status is completed. The record gives a start date of 2006-06 and a primary completion date of 2007-11. The sponsor is University Medical Centre Ljubljana. The registry does not report the randomization procedure, allocation concealment, or further operational details of the trial conduct.

The active treatment comparison was doxycycline versus cefuroxime axetil in adults with erythema migrans. The record identifies no masking; participants and investigators therefore were not masked according to the posted design description. The primary outcome was assessed at 14 days post inclusion. Its stated analysis population was participants who followed the protocol and were eligible for analysis. The number actually included in that analysis, the criteria used to define protocol adherence, and the handling of participants with missing endpoint data are not reported in the registry record.

The trial also included controls without Lyme disease to address whether symptoms reported after erythema migrans treatment were more frequent than similar symptoms among controls. The registry lists follow-up outcomes at 6 months and 12 months, as well as selected subjective symptoms at an examination at 12 months. These symptom comparisons address a distinct question from the randomized comparison of the two antibiotics. The record does not report how controls were selected or whether their characteristics were matched to those of patients.

The summary states that the treatment comparison used clinical and bacteriological criteria and a noninferiority testing approach. The noninferiority margin, planned sample-size justification, and detailed statistical analysis plan are not reported in the registry record. No reported analyses are listed for the posted secondary outcomes.

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.

Before assignment: 113/398 patients were ineligible due to: * receiving antibiotic with known anti-borrelial activity (73) * multiple erythema migrans (16) * history of Lyme disease (12) * immunocompromising condition (4) * serious adverse reaction to study drugs (3) * pregnancy or lactation (4) * erythema migrans accompanied by meningitis (1)

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants who followed the protocol were eligible for 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 Objective Lyme Disease Manifestations and Post-Lyme Disease Symptoms at 14 Days, measured over at 14 days post inclusion.

The primary endpoint counts participants with objective manifestations of Lyme disease and/or post-Lyme disease symptoms at 14 days post inclusion. The objective manifestations listed in the registry are persistence of erythema migrans or extracutaneous cardiac, nervous, or skeletal Lyme disease manifestations. The endpoint description applies to patients treated for solitary erythema migrans. The outcome is a participant count rather than a continuous measure, and the posted arm results give both the number of participants with an event and the number in each arm.

This combined endpoint brings together clinical findings and symptoms. It was selected to assess treatment outcomes using clinical and bacteriological criteria, as described in the trial summary. A combined outcome can capture more than one kind of unfavorable finding, but its interpretation depends on the components included and how they are assessed. The registry does not report the component-specific results, so the overall counts do not show how many participants had persistent erythema migrans, extracutaneous manifestations, symptoms, or overlapping findings. The record also does not describe the bacteriological criteria or their results separately.

The posted endpoint is measured at a defined follow-up time, which allows the trial to compare the reported event frequency between treatment arms at that time. The registry states that participants who followed the protocol were eligible for analysis; the detailed analysis population and missing-data handling are not reported.

7. Results Posted in the Registry

• Cefuroxime Axetil: 19.3% (27/140) versus 20.7% (30/145) on control; risk difference -1.4 percentage points (95% CI -10.7 to 7.9), risk ratio 0.93 (0.59–1.48); unadjusted two-proportion z-test p = 0.767.

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.

New or Increased Symptoms Since Erythema Migrans in Patients and Controls at 6 Months.

• 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:
  • Patients: 4.6% (9/194) versus 6.8% (16/236) on control; risk difference -2.1 percentage points (95% CI -6.5 to 2.2), risk ratio 0.68 (0.31–1.51); unadjusted two-proportion z-test p = 0.345.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patients and the control. The interval gives the range of effects that remain compatible with the data.

New or Increased Symptoms Since Erythema Migrans in Patients Controls at 12 Months.

• 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:
  • Patients: 2.2% (5/230) versus 9.4% (21/224) on control; risk difference -7.2 percentage points (95% CI -11.5 to -2.9), risk ratio 0.23 (0.09–0.60); 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 Patients than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Selected Subjective Symptoms in Patients and Control Subjects

• 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:
  • Patients: 77.4% (178/230) versus 80.8% (181/224) on control; risk difference -3.4 percentage points (95% CI -10.9 to 4.1), risk ratio 0.96 (0.87–1.05); unadjusted two-proportion z-test p = 0.372.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patients and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address symptoms at follow-up and selected subjective symptoms, rather than the primary endpoint’s combination of objective Lyme disease manifestations and post-Lyme disease symptoms at 14 days. Their comparisons also use patients and controls, not solely the randomized doxycycline and cefuroxime axetil groups. They therefore provide context about the symptom question described in the trial summary, but they are not direct replications of the primary active-treatment comparison.

Across the posted outcomes, the estimated differences are not all alike in direction or precision. The registry reports a statistically notable unadjusted comparison for new or increased symptoms at 12 months, while the comparisons for symptoms at 6 months and selected subjective symptoms at 12 months have unadjusted intervals that include no difference. This pattern should be read as a set of exploratory signals rather than a single consistent finding across all symptom measures. Each outcome has its own measurement, follow-up, analysis population, and uncertainty.

The secondary comparisons cannot resolve the primary noninferiority question because they concern different endpoints and, in some cases, different groups. Nor do they establish that differences in symptoms are caused by the treatment comparison. The registry lists no reported analyses for these secondary outcomes, and no multiplicity procedure is reported. When many outcomes are examined, the chance of at least one apparently unusual result can rise. Unadjusted secondary results consequently carry less weight than a prespecified, appropriately analyzed primary result, particularly when the analysis plan and multiplicity handling are unavailable.

The registry summary explains that controls were included because similar background symptoms occur in the general population and because the significance of post-Lyme disease symptoms was a subject of controversy. The control comparisons speak to that stated motivation, but the record does not report control-selection procedures, baseline comparability, or adjusted analyses. The observed symptom pattern should therefore be interpreted in the context of these limitations, not as a complete explanation of the origin or meaning of symptoms.

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

• New or Increased Symptoms Since Erythema Migrans in Patients and Controls at 6 Months.
• New or Increased Symptoms Since Erythema Migrans in Patients Controls at 12 Months.
• Selected Subjective Symptoms in Patients and Control Subjects

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

A risk difference subtracts the event risk in the reference group from the event risk in the comparison group. In the posted primary comparison, the reference is doxycycline and the comparison is cefuroxime axetil. A negative estimate means the observed event risk was lower in the cefuroxime axetil group; a positive estimate would mean it was higher. The estimate is -0.014. It is an absolute difference on the risk scale, not a relative percentage change. The confidence interval describes uncertainty around that estimated difference.

How should the confidence interval be read?

A confidence interval is a range of values compatible with the observed data under the assumptions of the analysis procedure. It conveys uncertainty about the estimated effect, rather than a range containing a fixed proportion of individual outcomes. For the primary risk difference, the interval extends from -0.107 to 0.079. Because it includes zero, the posted data are compatible with no risk difference as well as with differences in either direction within the interval. The interval’s width also matters: the estimate should not be read as precise simply because its central value is near zero.

What does the p-value contribute?

The unadjusted p-value is 0.767. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. 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 registry lists an unadjusted result and does not report a multiplicity adjustment for this outcome. The p-value therefore should be read alongside the event counts, effect estimate, and confidence interval, not in isolation.

How do relative measures differ?

The risk ratio compares the event risk in one group with the risk in the reference group. The odds ratio compares event odds rather than risks. These measures use different scales from the risk difference, so their numerical values are not interchangeable. The primary risk ratio is 0.932, with a confidence interval from 0.585 to 1.484; the primary odds ratio is 0.916, with a confidence interval from 0.512 to 1.638. For both relative measures, the null value is one. The confidence intervals include that value. Relative measures can be useful for expressing comparative effects, but the event counts and absolute risks remain important for understanding what was observed in the trial groups.

Why does the analysis population matter?

The registry says participants who followed the protocol were eligible for analysis of the primary outcome. This is a description of an analysis population, but it does not give the number included or a detailed definition of following the protocol. A per-protocol analysis can differ from an analysis that retains all randomized participants in their assigned groups. Excluding participants after randomization can affect comparability if the exclusions are related to treatment or outcome. The registry does not report an intention-to-treat result, the exclusions from the primary analysis, or reasons for missing outcomes, so the potential impact cannot be assessed from the posted record.

What is the significance of the stated noninferiority aim?

In general, a noninferiority trial asks whether the effect of a comparison treatment is not worse than the reference treatment by more than a prespecified margin. The margin defines what amount of difference would be considered acceptable for the statistical test; it must be specified before interpreting the result. The registry summary names noninferiority as the approach for comparing treatments, but the margin and formal test result are not reported in the registry record. A small estimated difference or a nonsignificant superiority test is not, by itself, proof of noninferiority.

What do the planning figures mean?

The planning illustrations use the observed effect as a reference and show hypothetical participant requirements for detecting stated fractions of that effect under the listed assumptions. These calculations are not a substitute for the trial’s original design rationale. General planning calculations depend on assumptions about the outcome, allocation, significance level, and target power. The registry gives its planning assumptions for these illustrations, but the trial’s own sample-size justification and original design assumptions are not reported. The planning figures should therefore be read as hypothetical design aids, not as evidence about how well the completed trial was powered.

All posted treatment comparisons are unadjusted. The registry does not report adjusted effect estimates, a prespecified analysis plan, or reported analyses for the secondary outcomes. The estimates are best understood as descriptive comparisons based on the posted counts and stated methods, with uncertainty reflected in their confidence intervals.

11. Confidence Intervals and Precision

The primary risk difference is -0.014, with a 95% confidence interval from -0.107 to 0.079. This interval includes zero and spans differences favoring either treatment. The central estimate alone is therefore an incomplete description: the interval indicates that the data do not tightly locate the treatment difference. Its limits should be interpreted on the absolute risk-difference scale, not as a relative change.

The relative measures tell a similar story about uncertainty. The risk ratio is 0.932, with a 95% confidence interval from 0.585 to 1.484, and the odds ratio is 0.916, with a 95% confidence interval from 0.512 to 1.638. Each interval includes its respective null value. These intervals do not demonstrate equivalence; they indicate that the posted data are compatible with a range of comparative effects.

Precision depends on the amount of information in the analysis, including the event counts and analysis denominators. The registry reports 30 events among 145 participants for doxycycline and 27 among 140 for cefuroxime axetil. Those are the denominators and counts attached to the primary results; overall enrollment is listed separately as 544. The registry does not report why the primary outcome denominators differ from overall enrollment, how missing outcomes were handled, or whether the confidence interval accounts for any features beyond the unadjusted comparison.

The reported interval does not address the clinical acceptability of possible differences. That judgment would require a prespecified margin or other interpretive criteria, which are not reported in the registry record. In particular, the confidence interval cannot answer the stated noninferiority question without the noninferiority margin.

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 for 80% power and participants per arm for 90% power. They are not total event counts. The registry’s stated assumptions 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 the stated fraction of the observed effect. These are planning assumptions for the illustrations; the trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the hypothetical number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the specified effect, if the planning assumptions hold and the effect is real. The 90% power column gives the corresponding hypothetical number per arm for a 90% chance. These are design targets, not estimates of the trial’s achieved power. This is not observed power.

Each planning row uses a different fraction of the observed effect as the effect to detect. Planning for 100% of the observed effect gives the smaller target effect only in the sense that it uses the full observed effect; planning for 75% or 50% of that effect asks the calculation to detect a smaller difference. Smaller effects generally require more participants to detect under otherwise unchanged assumptions. The figures are illustrations based on the observed estimate, not a claim that the observed effect is the true effect or that the original trial was designed around it.

The curve should be read as a visual representation of how the planning requirement changes as the target effect changes, under the same stated assumptions. It does not add independent evidence about treatment outcomes. The registry does not report that these calculations were used to determine the trial’s enrollment.

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 = 0.207; treatment proportion p₁ = 0.193; average p̄ = 0.200.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5656 = 1.1085.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5655 = 0.4759.
4. n = (1.1085 + 0.4759)² / (-0.0140)² = 12,735.6, rounded up to 12,736 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 <- 0.206896551724138                          # control proportion
p1 <- 0.192857142857143                          # 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(1518192)
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 = 12,736 (80% power), 17,049 (90% power)
 75% of observed effect: n per arm = 22,791 (80% power), 30,510 (90% power)
 50% of observed effect: n per arm = 51,614 (80% power), 69,095 (90% power)
power.prop.test: 12735.6 
Simulated power at n = 12,736 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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, and reports that the trial had 8 outcome measures. It posts three secondary outcomes in the available results. The record lists 0 reported analyses for those secondary outcomes. It does not state how the primary endpoint was selected in relation to the other outcomes, whether outcome hierarchies were prespecified, or whether the investigators planned to adjust for multiple comparisons.

Multiplicity matters because examining several endpoints, timeframes, or comparisons creates more opportunities for an apparently notable result to occur by chance. An unadjusted p-value describes an individual comparison under its assumptions; it does not account for a collection of tests. The 12-month symptom comparison has an unadjusted p-value of <0.001, but the registry does not report a multiplicity adjustment or a prespecified testing sequence. That result should not be treated as if it had been interpreted within a documented family-wise analysis plan. The other secondary results also need to be read as part of the overall set of outcomes rather than as independent confirmatory tests.

The primary comparison is reported as an unadjusted analysis. The summary describes a noninferiority testing approach, but the margin and formal analysis details are not reported in the registry record. The original statistical analysis plan, interim analyses, and the rationale for the analysis populations are also not reported. These omissions limit assessment of whether the posted analyses follow a prespecified plan.

For the primary outcome, the registry says that all participants who followed the protocol were eligible for analysis. It does not report the actual number analyzed under that criterion, the number excluded, the reasons for exclusion, or an intention-to-treat analysis. Missing outcome counts, the approach to missing data, and the sensitivity of results to alternative assumptions are not reported. Without those details, it is not possible to assess whether missingness or post-randomization exclusions could have influenced the comparison. These reporting gaps do not establish that the analyses were biased; they mean that the registry record does not allow their impact to be evaluated.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0.7% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports 0 serious adverse events among 145 participants at risk in the doxycycline group, 0 among 140 participants at risk in the cefuroxime axetil group, and 0 among 259 controls at risk. No serious adverse event terms are listed. The death counts are not reported in the registry record.

These figures describe the serious adverse event information posted for the stated groups; they do not establish that no serious events occurred outside the reported record or that all safety outcomes were captured. The registry also lists 21 participants with other adverse events in each treatment group and 0 among controls, but does not provide specific terms in the posted safety information. The meaning of those counts depends on the definitions, collection procedures, and follow-up completeness, which are not reported in the registry record.

Zero posted serious adverse events should not be interpreted as proof of absence of risk. The record does not provide detailed adverse-event methods, severity gradings beyond the serious-event category, causal assessments, or a fuller account of safety monitoring. These registry entries are a limited summary and do not support broader conclusions about comparative safety.

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

The primary results describe a small estimated difference in the observed event risks at 14 days, with a confidence interval that includes zero and spans effects in either direction. They do not show a statistically clear difference in the unadjusted comparison. This is not the same as showing that the treatments are equivalent, or that either treatment is noninferior. The stated noninferiority objective cannot be assessed without the margin and formal test details, which are not reported in the registry record.

The endpoint combines persistent erythema migrans, extracutaneous manifestations, and/or post-Lyme disease symptoms. As a result, the total event count does not identify which component accounted for events or whether a participant had more than one component. Component-specific outcomes are not reported. The result therefore describes the combined endpoint, not every clinical feature considered separately.

The secondary symptom outcomes address a related but distinct issue: how often patients and controls reported new or increased symptoms after erythema migrans treatment. Those comparisons are not interchangeable with the randomized antibiotic comparison. Their interpretation is limited by the unadjusted analyses, lack of reported multiplicity procedures, and absence of details on control selection and baseline comparability.

Random allocation is an important design feature for comparing assigned treatments, but the registry record alone does not give enough detail to assess every part of trial conduct. It does not report the randomization method, allocation concealment, endpoint-assessment procedures, missing-data methods, or detailed analysis populations. The posted findings should consequently be understood as a registry-level account of the reported outcomes, not as a complete evaluation of all design and analysis decisions.

The results concern the participants, endpoint definitions, and follow-up described in this record. They do not establish what would happen in other populations or settings, and they do not provide treatment advice. The interpretation remains bounded by the uncertainty in the estimates and the details that are not reported.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between failing to demonstrate a difference and demonstrating that treatments are sufficiently similar. The primary risk difference is close to zero, and its unadjusted p-value is not small, but the confidence interval still covers a range of possible differences. A noninferiority conclusion requires a prespecified margin and a comparison of the confidence interval with that margin. Although the registry summary identifies a noninferiority approach, the margin and formal test are not reported. This makes the record a practical illustration of why a nonsignificant superiority comparison cannot stand in for a noninferiority analysis.

The endpoint also illustrates how composite outcomes can simplify a comparison while combining clinically distinct events. The primary count includes objective manifestations and/or symptoms, yet component-specific counts are not posted. Without those counts, readers cannot see whether the overall result reflects one component, multiple components, or overlap. The endpoint definition is therefore essential to understanding what the estimate represents.

The trial’s symptom comparisons add a separate statistical challenge. Controls were included because the trial summary raises the possibility of similar background symptoms in people without Lyme disease. Comparing symptom reports in patients and controls can address that question, but interpretation depends on how controls were selected and whether groups were comparable. Those details are not reported in the registry record. The secondary comparisons also involve multiple outcomes and follow-up times, while no multiplicity method is reported. This reinforces the need to distinguish exploratory patterns from confirmatory results.

Finally, the registry separates overall enrollment from the denominators reported for the primary endpoint, without explaining the difference. That gap highlights why analysis populations, exclusions, and missing-data reporting are important parts of statistical interpretation. The posted estimates are informative, but their precision and meaning depend on details that the registry record does not include.

18. Limitations

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

The posted primary outcome denominators are smaller than the overall enrollment listed in the registry, and the record does not explain the difference. It does not state how many participants were randomized to each treatment, how many contributed to the primary analysis, or why other enrolled participants may not appear in the primary arm results. The primary analysis is described as including participants who followed the protocol, but the protocol-adherence criteria and resulting analysis population are not specified.

The registry does not report missing outcome counts, methods for handling missing observations, or sensitivity analyses. These omissions make it difficult to assess whether incomplete follow-up or exclusions could affect the estimated treatment comparison. The record also does not report an intention-to-treat result, which would provide a different perspective on the randomized assignment comparison.

The trial is described as open-label, and the registry does not report whether endpoint assessors were masked or how clinical manifestations and symptoms were assessed. Because the endpoint includes symptom reports as well as objective manifestations, the absence of assessment details limits evaluation of possible measurement differences between groups. Component-specific primary outcome results are not reported, so the combined event count cannot be decomposed.

The summary identifies a noninferiority approach, but the margin, original sample-size justification, and formal analysis plan are not reported. The record also does not report interim analyses or a multiplicity strategy. For the symptom comparisons with controls, selection methods and baseline comparability are not described. Finally, the safety record lacks detailed event terms and reports deaths as not reported. These limitations concern what can be evaluated from the registry record; they do not establish that any particular bias or safety issue occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Doxycycline and Cefuroxime Axetil for Treatment of Erythema Migrans: Clinical and Microbiological Outcome — NCT01518192.
• Registry record last updated 2012-01-25; status last verified 2011-12.
• Results first posted 2012-01-25.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01518192 is a completed, randomized, open-label, parallel-group Phase 4 trial sponsored by University Medical Centre Ljubljana. The registry lists enrollment of 544 and compares doxycycline with cefuroxime axetil for adults with erythema migrans. The primary outcome counts participants with objective Lyme disease manifestations and/or post-Lyme disease symptoms at 14 days post inclusion.

The posted primary results are 30 of 145 participants for doxycycline and 27 of 140 for cefuroxime axetil. The risk difference for cefuroxime axetil versus doxycycline is -0.014, with a 95% confidence interval from -0.107 to 0.079 and an unadjusted p-value of 0.767. The summary describes a noninferiority approach, but the margin and formal noninferiority analysis are not reported in the registry record.

Secondary symptom outcomes compare patients with controls at follow-up. The registry does not report analyses for these outcomes or a multiplicity procedure. It also does not report the primary analysis’s missing-data handling, detailed population counts, or the trial’s original sample-size justification.