A Study of the Cobas® Liat CT/NG/MG Test Versus Current Standard Practice for Managing Participants at Increased Risk of Sexually Transmitted Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Cobas® Liat CT/NG/MG Test Versus Current Standard Practice for Managing Participants at Increased Risk of Sexually Transmitted Infections (NCT06369220), a randomized na study. The primary outcome is Percentage of Participants Given Inappropriate Treatments for All Pathogens Combined (CT, NG, and MG).

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, parallel-group study with no masking. It lists an enrollment of 331 and identifies Hoffmann-La Roche as the sponsor. The study compared a point-of-care diagnostic testing strategy with clinician standard practice for managing participants at increased risk of sexually transmitted infections. The phase is listed as NA.

In the point-of-care arm, clinicians evaluated participants and were provided with cobas® Liat CT/NG/MG results, which they could use in clinical decisions. In the standard-of-care arm, clinicians evaluated participants according to standard practice. The comparison therefore concerns clinical management under these strategies, not simply the diagnostic performance of a test considered in isolation.

The primary outcome was inappropriate treatment for CT, NG, and MG combined on Day 1. The registry defines the primary evaluable population as enrolled participants with a valid EL-PCR result for each pathogen. The posted arm results list 160 participants for the point-of-care arm and 170 for standard of care; these are the arm denominators associated with the posted primary results.

The registry also lists outcomes concerning inappropriate treatment for each pathogen separately, clinician satisfaction and confidence, and participant satisfaction and confidence. The record does not report the original sample-size justification, detailed statistical analysis plan, or a fuller account of the randomization procedure. Those details should not be inferred from the posted comparison or the planning illustrations.

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: The clinicians referred to as any health care professional (e.g., doctor, provider, pharmacist, nurse, etc.) involved with performing diagnostic tests on participants, interpreting the results, and providing participant care were not enrolled in the study. No participant flow/baseline/safety data was collected for the clinicians. The clinician only completed the Clinician Satisfaction with Diagnostic Test Questionnaire (CSDT-Q).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Evaluable population included enrolled participants with a valid result for each of the 3 pathogens by EL-PCR.

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.

Population: Evaluable population included enrolled participants with a valid result for each of the 3 pathogens by external laboratory-polymerase chain reaction (EL-PCR).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Given Inappropriate Treatments for All Pathogens Combined (CT, NG, and MG), measured over On the day of the medical encounter (Day 1).

The primary endpoint is the percentage of participants given inappropriate treatments for all pathogens combined, assessed on the day of the medical encounter (Day 1). It combines inappropriate management related to CT, NG, and MG rather than treating each pathogen as the primary question separately.

The registry defines inappropriate treatment by reference to CDC recommendations and pathogen-specific results from EL-PCR testing. Over-treatment includes giving two or more antibiotics when only one is necessary, or giving any unnecessary antibiotics. Under-treatment means failing to provide pathogen-appropriate antimicrobials, alone or in combination. The endpoint can therefore capture errors in either direction: treatment that was unnecessary or excessive, and treatment that did not cover the identified pathogen appropriately.

This outcome is used to compare the clinical utility of the point-of-care testing strategy with standard practice. It reflects treatment decisions made in the encounter, interpreted against pathogen results, rather than a measure of test accuracy alone. The evaluable population requires a valid result for each of the three pathogens, so the posted primary percentages describe that specified analysis population rather than necessarily every enrolled participant. The registry does not report further detail about how participants without the required valid results were handled.

7. Results Posted in the Registry

• Point of Care Arm: 11.9% (19/160) versus 21.8% (37/170) on control; risk difference -9.9 percentage points (95% CI -17.9 to -1.9), risk ratio 0.55 (0.33–0.91); unadjusted two-proportion z-test p = 0.017.

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.

Percentage of Participants Given Inappropriate Treatment for CT Infection

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Point of Care Arm: 10.6% (17/160) versus 15.9% (27/170) on control; risk difference -5.3 percentage points (95% CI -12.5 to 2.0), risk ratio 0.67 (0.38–1.18); unadjusted two-proportion z-test p = 0.160.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Point of Care Arm and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Given Inappropriate Treatment for NG Infection

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Point of Care Arm: 2.5% (4/160) versus 4.7% (8/170) on control; risk difference -2.2 percentage points (95% CI -6.2 to 1.8), risk ratio 0.53 (0.16–1.73); unadjusted two-proportion z-test p = 0.285.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Point of Care Arm and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Given Inappropriate Treatment for MG Infection

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Point of Care Arm: 1.9% (3/160) versus 6.5% (11/170) on control; risk difference -4.6 percentage points (95% CI -8.8 to -0.3), risk ratio 0.29 (0.08–1.02); unadjusted two-proportion z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Point of Care Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the pathogen-specific inappropriate-treatment outcomes, the observed percentages were lower in the point-of-care arm than in standard care. The estimates are not equally precise, and the strength of statistical evidence varies across these outcomes. In particular, the pathogen-specific comparisons do not all provide similarly clear evidence of an arm difference. The posted values should be interpreted as secondary context for the combined primary result, not as repeated confirmations of it.

The registry also lists clinician and participant satisfaction and confidence outcomes. Their presence broadens the study’s focus beyond inappropriate treatment, but the record does not provide their results in the posted outcomes. They therefore cannot be used to infer whether either group was more satisfied or confident.

Secondary findings can help identify whether the overall pattern appears consistent across components, but multiple outcomes create more opportunities for apparently notable results to occur by chance. The record does not report a multiplicity adjustment or a hierarchy controlling the interpretation of secondary comparisons. Their p-values should therefore be treated as unadjusted evidence, with less weight than the primary comparison, and not as independent definitive conclusions.

The combined primary endpoint and pathogen-specific outcomes answer related but distinct questions. The combined result summarizes inappropriate treatment across CT, NG, and MG in the defined evaluable population. The secondary pathogen-specific results can suggest where that combined pattern may or may not be reflected, but they do not establish why the combined result arose. Nor can the registry’s listed satisfaction and confidence outcomes be interpreted without their outcome data.

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

• Percentage of Participants Given Inappropriate Treatment for CT Infection
• Percentage of Participants Given Inappropriate Treatment for NG Infection
• Percentage of Participants Given Inappropriate Treatment for MG Infection
• Percentage of Clinicians With Satisfaction Scores for SOC and POC According to the Clinician Satisfaction With Diagnostic Test Questionnaire (CSDT-Q)
• Percentage of Clinicians With Confidence Scores for SOC and POC According to the CSDT-Q
• Percentage of Participants With Satisfaction Scores for SOC and POC According to the Patient Satisfaction With Diagnostic Test Questionnaire (PSDT-Q)
• Percentage of Participants With Confidence Scores for SOC and POC According to the PSDT-Q

9. Statistical Interpretation

10. Statistical Methods Explained

Binary outcome and percentages. The primary endpoint is binary at the participant level: a participant either met the registry definition of inappropriate treatment or did not. An arm percentage expresses the observed proportion meeting that definition among participants included in the relevant analysis. Such a percentage is easy to interpret, but its precision depends on the number of participants and the frequency of the outcome, and it does not by itself describe the uncertainty around the estimate.

Risk difference. A risk difference compares the proportions in two arms by subtracting one arm’s risk from the other. The recalculated value is -0.099 for the point-of-care arm relative to standard of care. A negative value means the observed proportion was lower in the point-of-care arm under this ordering of the comparison. Risk differences retain the outcome’s absolute scale, which makes them useful for understanding the size and direction of an arm contrast. The registry’s sponsor analysis also reports a difference of 9.88; its positive sign reflects the way that comparison is presented. The record does not attach a p-value to that difference analysis.

Relative risk. A relative risk compares the proportion in one arm with the proportion in the reference arm. A value below 1 indicates a lower observed proportion in the numerator arm than in the reference arm; a value of 1 represents equal proportions. The sponsor reports a relative risk of 0.55 for the primary comparison. A relative measure gives a different perspective from an absolute difference, so the two should be read as complementary descriptions rather than interchangeable quantities.

Confidence intervals. A confidence interval describes the range of estimates reasonably compatible with the data and the method used, under repeated sampling assumptions. It communicates precision as well as direction. An interval that includes the null value—0 for a difference or 1 for a relative risk—does not provide clear evidence of a difference by that interval criterion. Excluding the null can support a statistical contrast, but it does not establish clinical importance or remove possible design and data limitations. General statistical explanation: intervals are not guarantees that a particular true value lies inside the reported range.

Chi-squared analysis and p-values. The sponsor’s posted primary relative-risk analysis is identified as chi-squared. A chi-squared test evaluates whether the observed categorical outcome distribution is compatible with equal proportions under its null hypothesis. The p-value describes how unusual a result at least as extreme as the observed one would be if that null hypothesis and the model assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of the observed difference. The sponsor reports p = 0.017; the unadjusted recalculation reports p = 0.017. These are not adjusted for multiplicity in the information reported.

Unadjusted recalculation. The recalculated risk difference, interval, and p-value are simple unadjusted comparisons based on the posted summary data. They are not a substitute for a full participant-level analysis or the sponsor’s analysis. The record indicates no discrepancy, so the sponsor’s reported result remains the primary reference for the sponsor’s own analysis. The registry does not report all details needed to reproduce the sponsor’s method independently, including a full analysis plan.

Why outcome definitions matter. This endpoint is defined against pathogen-specific EL-PCR results and CDC recommendations. Its classification depends on whether treatment was unnecessary, excessive, or insufficient for the identified pathogen. The definition makes clear that both over-treatment and under-treatment count, but the record does not report separate primary endpoint components or how often each component occurred. The combined result should therefore be interpreted as an overall measure of inappropriate treatment, not as a direct estimate for every component or pathogen.

Randomization and interpretation. Random allocation can help make groups comparable at baseline on average, supporting a fairer comparison of management strategies. It does not guarantee identical groups, ensure complete outcome data, or correct all implementation differences. The record specifies randomized parallel groups and no masking, but it does not report detailed allocation procedures or blinding of outcome assessment. These omissions limit assessment of how the design was implemented; they are not grounds to assume a particular procedure.

11. Confidence Intervals and Precision

The primary arm percentages are 11.88% for point-of-care testing and 21.76% for standard of care. The sponsor’s relative-risk estimate is 0.55, with a 95% confidence interval from 0.33 to 0.91. The interval is entirely below the relative-risk null value of 1, indicating that the posted sponsor analysis is compatible with a lower proportion in the point-of-care arm under its comparison.

The recalculated risk difference is -0.099, with a 95% confidence interval from -0.179 to -0.019. This interval is entirely below the risk-difference null value of 0 and places the estimated contrast on the lower side for the point-of-care arm. The agreement in direction between relative and absolute measures helps readers distinguish the observed contrast from its uncertainty.

Confidence intervals are not equally narrow or equally informative for every outcome. They reflect the variability in the observed data and the method used to construct them. For secondary comparisons, the intervals are wider in relation to their estimates, especially where events are sparse; that reduces precision and makes the exact magnitude uncertain. The primary interval also allows a range of possible effects, rather than identifying a single definitive magnitude.

Statistical precision is distinct from clinical importance. The registry does not report a threshold for a clinically meaningful change in inappropriate treatment, so the intervals cannot be judged against a stated minimum important effect. They also do not describe uncertainty from unreported elements such as missing-data handling or analytic choices. The confidence intervals should be read as uncertainty under the posted analysis, not as a complete accounting of every uncertainty in the study.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations calculated from the observed effect, not the trial’s original sample-size justification. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of participants per arm needed for an analysis to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These values are design aids, not findings about the probability that the completed study detected an effect. They are not observed power.

The rows represent planning for 100%, 75%, and 50% of the observed effect. The smaller the effect selected for planning, the more participants are needed to detect it at the stated power level. For the primary comparison, the posted illustrations list 224 and 299 participants per arm when planning for 100% of the observed effect; 421 and 564 for 75%; and 999 and 1,337 for 50%, for 80% and 90% power respectively.

These figures are conditional on the specified assumptions and observed effect. They do not establish that the study was designed with those targets, nor do they show what its original design team expected. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

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 = 0.218; treatment proportion p₁ = 0.119; average p̄ = 0.168.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5290 = 1.0368.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5243 = 0.4413.
4. n = (1.0368 + 0.4413)² / (-0.0989)² = 223.4, rounded up to 224 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 <- 0.217647058823529                          # control proportion
p1 <- 0.11875                          # 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(6369220)
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 = 224 (80% power), 299 (90% power)
 75% of observed effect: n per arm = 421 (80% power), 564 (90% power)
 50% of observed effect: n per arm = 999 (80% power), 1,337 (90% power)
power.prop.test: 223.4 
Simulated power at n = 224 per arm: 0.806 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis reports a relative risk of 0.55 (95% confidence interval 0.33 to 0.91) using a chi-squared method, with p = 0.017. The sponsor also reports a difference of 9.88 with a 95% confidence interval from 1.78 to 17.84 and classifies the analyses as superiority. The posted arm percentages are 11.88% for point-of-care testing and 21.76% for standard of care.

The simple unadjusted recalculation gives a risk difference of -0.099 (95% confidence interval -0.179 to -0.019) and p = 0.017. The recalculated relative-risk summary is 0.546, with an interval from 0.328 to 0.908. The recalculation and sponsor analysis point in the same direction and the registry record identifies no discrepancy. The sponsor’s own analysis therefore remains the reference for the sponsor-reported result; the recalculation is an independent, unadjusted check based on posted summary statistics, not a replacement analysis.

Differences in presentation and rounding can make the reported values look slightly different. The sponsor’s difference is expressed with the opposite sign direction from the recalculated risk difference, consistent with comparing the arms in a different order. The registry does not report enough detail to reconstruct every analytic choice behind the sponsor’s output, so the recalculation should not be treated as proof that all analysis procedures were identical.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, including pathogen-specific treatment outcomes and satisfaction and confidence measures. Testing several outcomes increases the chance that at least one comparison will appear statistically notable by chance, even when the comparisons are considered together. This is the general multiplicity problem: the evidential meaning of an individual unadjusted p-value depends partly on how many questions were examined and how those questions were selected and interpreted.

The record does not report whether the analysis plan used a formal multiplicity adjustment, a testing hierarchy, or another strategy to control error across outcomes. It also does not report interim analyses or a complete prespecified statistical analysis plan. Their absence from the registry record does not establish that such procedures did not occur; it means they cannot be assessed from this record.

The primary endpoint is the clearest central comparison in the registry. Secondary outcomes are useful for context, but their unadjusted results should be regarded as exploratory or supportive unless a prespecified analysis strategy is documented. The reported superiority classifications do not by themselves show how multiplicity was handled across the family of endpoints.

The primary evaluable population required a valid EL-PCR result for each pathogen. The registry does not report how many enrolled participants lacked a valid result for one or more pathogens, the reasons for missing results, or the procedures used to address missing outcome data. It also does not specify whether the primary analysis was intention-to-treat, per-protocol, or another population definition beyond the stated evaluable-population criterion. These are important limits when assessing whether the analyzed participants represent everyone randomized and how robust the result may be to missingness.

Because the record does not report those details, the handling of missing data and the effect of any analysis-population choices cannot be evaluated. The posted percentages should be read within the population definition that is explicitly stated, without assuming an unreported imputation method or analysis strategy.

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 0% reporting threshold.

The registry reports zero serious adverse events among 160 participants at risk in the point-of-care arm and among 170 participants at risk in the standard-of-care arm. It also reports zero other adverse events in each arm and zero deaths in each arm. No top serious adverse-event terms are listed.

These figures describe the safety events posted in the registry record; they do not establish that no adverse events occurred outside the recorded categories, or that the strategies have no safety risks. The event counts are zero in the reported groups, but the record does not provide additional detail about event definitions, collection procedures, follow-up beyond the stated encounter context, or independent adjudication. The primary question concerns treatment appropriateness on Day 1, so the safety figures should be understood as separate reported information rather than an assessment of longer-term safety.

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

The primary result shows a lower observed percentage of inappropriate treatment in the point-of-care arm than in standard care among participants included in the defined evaluable population. The sponsor’s relative-risk analysis and the unadjusted recalculation of the risk difference both point in that direction, and their confidence intervals exclude their respective null values. This is evidence of an arm difference in the posted primary comparison under the reported analyses.

The result does not mean that every participant in the point-of-care arm received appropriate treatment, nor that the diagnostic test by itself determined clinical decisions. The registry says clinicians could choose whether to base decisions on point-of-care results. It also does not show that all inappropriate treatment was prevented or identify which pathogen or type of treatment decision was responsible for the combined outcome.

The endpoint concerns treatment decisions on Day 1, benchmarked against pathogen-specific EL-PCR results and CDC recommendations. It does not directly measure subsequent infection outcomes, transmission, longer-term health, or the diagnostic accuracy of the test as a stand-alone measure. Nor does it establish the result in populations or clinical settings not described in the registry.

Statistical evidence should be separated from clinical importance and generalizability. The record does not state a threshold for a clinically meaningful difference, and the confidence interval leaves uncertainty about the magnitude. The study is randomized, but the registry does not provide every detail needed to assess allocation implementation, missing-data handling, multiplicity, or the full analysis plan. The findings are best understood as a comparison of the posted management strategies for the specified outcome and analysis population, with those limitations in view.

18. Why This Trial Matters Statistically

This trial raises a statistical question that is broader than whether a diagnostic test detects pathogens: can access to point-of-care results be associated with different treatment decisions during the clinical encounter? The primary endpoint addresses that question by judging over-treatment and under-treatment against pathogen-specific results and recommendations. It therefore links diagnostic information with a decision outcome rather than reporting test performance alone.

The combined endpoint is useful because it gives a single primary summary across CT, NG, and MG. At the same time, a combined outcome can conceal variation among its components. The separately listed pathogen-specific outcomes are relevant context, while their secondary status and multiplicity mean they should not be treated as equal in evidential weight to the primary comparison.

The registry also illustrates why effect measures and uncertainty should be read together. Percentages describe observed arm outcomes; the risk difference expresses an absolute contrast, and the relative risk expresses a comparison on a relative scale. Confidence intervals show that neither estimate is perfectly precise. Using more than one measure helps readers understand direction and scale without mistaking a p-value for an effect magnitude.

Finally, the record makes the distinction between a trial result and a planning calculation important. Illustrative sample-size requirements based on the observed effect are not the design assumptions that governed the completed study and are not observed power. Keeping those concepts separate helps prevent retrospective planning values from being misread as evidence about how adequately the trial was originally designed.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the detailed randomization procedures, allocation concealment, or whether outcome assessment was masked. The study is listed as randomized and unmasked, but the record does not establish how these design features were implemented. Because the intervention involves information available to clinicians, the observed comparison is a strategy comparison that includes clinician decisions, not an isolated estimate of test performance.

The primary analysis population required valid EL-PCR results for each pathogen. The record does not state how many enrolled participants were excluded from that population, why results may have been invalid or missing, or how missing data were handled. This limits assessment of selection and of whether the posted results represent all randomized participants.

The endpoint combines under-treatment and over-treatment across three pathogens. The registry provides definitions but does not report primary component counts or separate estimates for the components. Consequently, the combined result cannot explain which type of inappropriate treatment drove the observed contrast. Pathogen-specific secondary outcomes offer related information, but they do not remove this limitation or establish the mechanism of the primary finding.

The record does not report a complete statistical analysis plan, the original sample-size rationale, interim-analysis procedures, or a multiplicity strategy. Nor does it report a clinically meaningful threshold for the primary outcome. These gaps constrain interpretation of secondary results, planning adequacy, and the practical importance of the estimated effect. The posted outcome is limited to the medical encounter day, so longer-term consequences are not addressed by the primary result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Cobas® Liat CT/NG/MG Test Versus Current Standard Practice for Managing Participants at Increased Risk of Sexually Transmitted Infections — NCT06369220.
• Registry record last updated 2026-07-13; status last verified 2026-06.
• Results first posted 2026-06-23.
• 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.

23. Record Summary

The registry describes a completed, randomized, parallel-group, unmasked comparison of point-of-care cobas® Liat CT/NG/MG testing with clinician standard practice. The study enrolled 331 participants and focused on inappropriate treatment for CT, NG, and MG on Day 1.

In the evaluable population, the posted primary percentages were 11.88% in the point-of-care arm and 21.76% in standard care. The sponsor reported a relative risk of 0.55 (95% confidence interval 0.33 to 0.91; p = 0.017). The unadjusted recalculation also indicated a lower observed proportion in the point-of-care arm, with no discrepancy identified by the record.

Interpretation is limited by unreported details concerning missing data, analysis populations, multiplicity, and the original statistical plan. The secondary results and safety counts provide additional registry information but do not alter the scope of the primary endpoint.