Rapid Diagnostics for Upper Respiratory Infections in the Emergency Department: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rapid Diagnostics for Upper Respiratory Infections in the Emergency Department (NCT02957136), a randomized na study. The primary outcome is Proportion of Patients Receiving Antibiotics or a Prescription for Antibiotics in the ED.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group clinical trial listed as completed. The registry describes single masking, but does not identify which participants or study personnel were masked. The phase is listed as NA. The sponsor was the University of California, Davis.

The rapid respiratory pathogen test arm received a nucleic acid amplification test plus usual care. Participants assigned to usual care received clinician-directed standard care, which could include no testing, point-of-care influenza testing, or delayed testing at an off-site laboratory. Thus, the comparator represents usual care rather than a single specified diagnostic procedure.

The registry lists enrollment of 194. The study began on 2016-12-08, and primary completion is recorded as 2018-04-30. The primary endpoint is a participant count for antibiotic receipt or an antibiotic prescription in the emergency department on Day 0. The arm denominators posted for that outcome are 93 and 98. The registry record does not explain how the enrollment figure relates to the endpoint denominators.

The registry describes the trial objective as assessing whether rapid testing affected antibiotic and anti-influenza medication use. It also lists outcomes concerning pathogen identification, influenza diagnosis, treatment, disposition, repeat visits and admissions, and lengths of stay. The trial protocol, allocation ratio, masking details, and the original design assumptions are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Proportion of Patients Receiving Antibiotics or a Prescription for Antibiotics in the ED, measured over Day 0.

The primary endpoint counts participants who received antibiotics or an antibiotic prescription in the emergency department on Day 0. It combines two related events: receiving an antibiotic during the encounter and leaving with a prescription. The registry does not give a more detailed operational definition, such as how prescriptions were classified or whether particular antibiotic indications were included.

This outcome addresses the trial’s stated question about the effect of rapid pathogen testing on antibiotic use. Prescribing is a clinical decision that could respond to diagnostic information, so comparing the number of participants with this outcome across randomized arms can describe whether the observed prescribing pattern differed between the study groups. The endpoint is binary at the participant level: each participant either had the recorded event or did not, while the posted arm results give the event count and the number assessed.

The measure does not, by itself, establish whether a prescription was appropriate, whether antibiotics were taken, or whether patients’ symptoms or later health outcomes changed. Appropriateness of anti-influenza treatment is listed separately as a secondary outcome; it is not the primary endpoint. The registry’s brief endpoint description does not report further definitions or adjudication procedures.

7. Results Posted in the Registry

• Rapid Respiratory Pathogen Test Arm: 21.5% (20/93) versus 33.7% (33/98) on control; risk difference -12.2 percentage points (95% CI -24.7 to 0.4), risk ratio 0.64 (0.40–1.03); unadjusted two-proportion z-test p = 0.060.

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.

Proportion of Patients With a Respiratory Pathogen Identified

• 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:
  • Rapid Respiratory Pathogen Test Arm: 65.6% (61/93) versus 20.4% (20/98) on control; risk difference 45.2 percentage points (95% CI 32.7 to 57.7), risk ratio 3.21 (2.12–4.88); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rapid Respiratory Pathogen Test Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Proportion of Patients With a Laboratory-confirmed Influenza Diagnosis

• 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:
  • Rapid Respiratory Pathogen Test Arm: 25.8% (24/93) versus 8.2% (8/98) on control; risk difference 17.6 percentage points (95% CI 7.2 to 28.1), risk ratio 3.16 (1.50–6.68); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rapid Respiratory Pathogen Test Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Proportion of Patients Receiving Appropriate Anti-influenza Treatment or Prescription

• 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:
  • Rapid Respiratory Pathogen Test Arm: 78.5% (73/93) versus 86.5% (32/37) on control; risk difference -8.0 percentage points (95% CI -21.8 to 5.8), risk ratio 0.91 (0.77–1.07); unadjusted two-proportion z-test p = 0.297.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rapid Respiratory Pathogen Test Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several points along the diagnostic and care pathway. The posted Day 0 results show a consistent direction for the two diagnostic outcomes: respiratory pathogens were identified more often, and laboratory-confirmed influenza was recorded more often, in the rapid-testing arm. The appropriate anti-influenza treatment or prescription outcome does not show the same clear separation; its unadjusted comparison is compatible with no difference. These outcomes describe different questions, so a change in diagnostic identification need not correspond directly to a change in treatment.

The primary endpoint concerns antibiotic receipt or prescription. The secondary pattern therefore adds context but does not resolve the uncertainty in the primary comparison. Increased identification of pathogens is a diagnostic outcome, whereas prescribing is a decision outcome. The registry also lists disposition, repeat emergency visits or admissions, mortality, guideline adherence, and lengths of stay, but numeric arm results for those outcomes are not reported in the registry record.

Unadjusted secondary comparisons carry less weight as a group because testing multiple outcomes creates more opportunities for apparently notable results to arise by chance. In general, a multiplicity plan can specify how to interpret several comparisons together; none is reported in the registry record. The secondary analysis entries are empty, and the record does not say which outcomes were prespecified for formal testing or whether any adjustment was planned.

Denominators also differ across outcomes. In particular, the usual-care denominator for appropriate anti-influenza treatment or prescription is 37, rather than the 98 used for the primary endpoint. The registry does not explain the eligibility or data-availability rules underlying that denominator. This limits direct comparison across outcomes and makes it important not to treat the secondary pattern as one unified estimate of the intervention’s effect.

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

• Proportion of Patients With a Respiratory Pathogen Identified
• Proportion of Patients With a Laboratory-confirmed Influenza Diagnosis
• Proportion of Patients Receiving Appropriate Anti-influenza Treatment or Prescription
• Proportion of Patients Discharged Home From the ED Versus Hospital Admission
• Proportion of Patients With All-cause or Respiratory Illness-related Repeat ED Visit, Hospital or ICU Admission, or Death Within 30 Days
• Proportion of of Patients With Clinician Adherence to Guidelines for the Treatment of Patients With Influenza (Recommendations for Use of Antivirals Only)
• Median Length of ED Stay
• Median Length of Hospital Stay

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the proportion with an event in one arm with the proportion in the other. It is expressed as the first arm’s event proportion minus the comparator arm’s event proportion. A negative value means the event was less frequent in the first arm as observed; a positive value means it was more frequent. For the primary endpoint, the reported comparison is rapid respiratory pathogen testing versus usual care. The calculation uses the posted counts and denominators and is unadjusted.

A risk difference is an absolute contrast. It is distinct from a risk ratio, which compares proportions as a ratio, and an odds ratio, which compares odds. Each measure expresses the same binary outcome on a different scale. Because the risk difference and its confidence interval are available for the posted comparisons, interpretation can stay on the absolute scale rather than switching among several measures.

What does the confidence interval add?

A confidence interval communicates the uncertainty around an estimate. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. For a risk difference, an interval that includes zero is compatible with no difference as well as with differences in either direction at the interval’s stated confidence level. The primary endpoint interval includes zero, so its estimate should not be treated as a settled separation between arms. The registry does not identify a confidence level in the outcome description; the standard interpretation of the reported interval is therefore general statistical context.

How should the p-value be read?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model were true. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The primary comparison’s unadjusted p-value is 0.06. That value does not cross the conventional 0.05 threshold, but the threshold alone does not decide whether an effect exists. The estimate, interval, endpoint, study conduct, and analysis plan all matter. The registry record does not report a prespecified threshold or the full analysis plan.

The secondary comparison for respiratory pathogen identification has p < 0.001, and the laboratory-confirmed influenza comparison has p = 0.001. The anti-influenza treatment comparison has p = 0.297. These are unadjusted comparisons. They do not account for the possibility of multiple statistical tests across outcomes.

Why does randomization matter?

Random assignment is intended to make the arms comparable, on average, with respect to factors that might affect outcomes. It supports a causal comparison when the design and conduct preserve the assigned groups and the analysis follows an appropriate plan. The registry identifies the study as randomized and parallel, but the allocation procedure, allocation ratio, analysis populations, and handling of departures from assignment are not reported in the registry record. Randomization alone does not guarantee balance in a particular trial or resolve uncertainty from limited data.

The primary comparison is based on participant counts. The arm denominators are not identical, which is accommodated by comparing proportions rather than raw counts. However, the registry does not explain the endpoint denominator relative to total enrollment. No model-based adjustment is reported, and no assumptions about covariates or clustering should be inferred.

What does over-dispersion mean in general?

Over-dispersion arises when observed variability is greater than a statistical model expects. It can affect standard errors and confidence intervals for outcomes such as counts or rates. The primary endpoint is posted as a binary participant count, and the record does not report an over-dispersion assessment or a model requiring such an adjustment. This concept is general context, not a claim about an analysis performed in this trial.

The reported calculations are unadjusted re-calculations from the posted summary counts. They do not replace an analysis specified in a protocol. The registry’s analysis entries are empty, and the original analysis plan, any covariate adjustment, and the treatment of missing observations are not reported in the registry record.

11. Confidence Intervals and Precision

The primary endpoint estimate points toward fewer participants with antibiotic receipt or a prescription in the rapid-testing arm, but the confidence interval includes zero. This means the posted data do not locate the risk difference precisely enough to exclude no difference at the interval’s stated level. The interval also permits effects on either side of zero, so the direction and magnitude should not be treated as certain.

Precision depends in part on the amount of information available, including the number of participants with outcome data and the frequency of the event. The primary comparison uses 93 participants in the rapid-testing arm and 98 in usual care. The registry lists enrollment of 194 but does not explain the relationship between enrollment and those endpoint denominators. The record also does not report whether the endpoint data were complete for all randomized participants.

The secondary comparisons have different degrees of precision. The intervals for pathogen identification and laboratory-confirmed influenza lie on the positive side of zero, whereas the interval for appropriate anti-influenza treatment includes zero. These interval patterns describe uncertainty, not certainty about a mechanism or a treatment decision. The anti-influenza treatment denominators are 93 and 37, and the reason for that difference is not reported in the registry record.

Confidence intervals do not capture every source of uncertainty. They do not account automatically for selective outcome reporting, deviations from the analysis plan, or multiple comparisons. The registry record does not provide enough information to assess those issues fully. Readers should consider the breadth of the intervals alongside the trial design and the missing analysis details.

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 participants across both arms. The calculations are illustrations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The rows consider detecting 100%, 75%, or 50% of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 211 participants per arm for 80% power and 282 participants per arm for 90% power. Planning for 75% of the observed effect gives 388 participants per arm for 80% power and 519 participants per arm for 90% power. Planning for 50% of the observed effect gives 900 participants per arm for 80% power and 1,205 participants per arm for 90% power.

In plain terms, a power column describes the chance, under the assumptions used for the calculation, of detecting an effect of the stated size if that effect is truly present. The 90% column uses a higher probability of detection than the 80% column and consequently gives larger participant requirements. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm.

These are planning illustrations, not observed power. They are not a retrospective measure of whether the completed trial “had enough power,” and they do not establish what sample size the investigators originally intended. The sample-size curve should be read as a visual expression of how the calculated requirement changes with the effect size under these assumptions; it does not add evidence about the trial’s observed treatment effect.

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 = 0.337; treatment proportion p₁ = 0.215; average p̄ = 0.276.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6321 = 1.2389.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6262 = 0.5270.
4. n = (1.2389 + 0.5270)² / (-0.1217)² = 210.6, rounded up to 211 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 <- 0.336734693877551                          # control proportion
p1 <- 0.21505376344086                          # 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(2957136)
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 = 211 (80% power), 282 (90% power)
 75% of observed effect: n per arm = 388 (80% power), 519 (90% power)
 50% of observed effect: n per arm = 900 (80% power), 1,205 (90% power)
power.prop.test: 210.6 
Simulated power at n = 211 per arm: 0.804 (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 record lists a primary outcome and several secondary outcomes, including diagnostic findings, treatment, disposition, subsequent health-care use, and length of stay. It does not report a statistical analysis plan, a hierarchy for testing outcomes, or a procedure for controlling the overall chance of false-positive findings across multiple comparisons. No multiplicity adjustment is reported for the posted unadjusted comparisons.

In general, when many outcomes or comparisons are examined, the chance that at least one appears statistically notable by chance can increase. This does not invalidate an individual result, but it makes isolated secondary p-values less conclusive unless the testing strategy was planned and interpreted in context. The primary comparison is also unadjusted in the available calculations; the registry does not state whether an adjusted primary analysis was planned or performed.

Missing-data procedures are not reported in the registry record. The record does not state how missing outcome observations were handled, whether participants with unavailable data were excluded, or whether sensitivity analyses were conducted. The primary endpoint denominators are 93 and 98, while total enrollment is listed as 194, and the record does not reconcile these figures. The appropriate anti-influenza treatment outcome uses 93 and 37 participants, with no explanation of the denominator difference.

The analysis populations are likewise not reported. It is not stated whether analyses followed intention-to-treat, per-protocol, or another population definition, or how participants with protocol deviations were treated. Randomization is documented, but a detailed account of how assigned groups were preserved in analysis is absent. Without these details, the posted count-based comparisons are useful descriptive evidence but cannot be confirmed as matching a prespecified primary analysis.

15. 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 93 participants at risk in the rapid respiratory pathogen test arm and zero among 98 at risk in usual care. It also reports zero other adverse events in each arm, using the same at-risk denominators. These counts describe events recorded in the registry; they do not establish that no event of any kind occurred outside the registry’s reporting definitions or observation procedures.

Deaths are recorded separately: one in the rapid-testing arm and zero in usual care. The registry does not report the cause of death or whether it was considered related to the intervention. It also does not provide further detail about event definitions, severity grading, timing, or follow-up procedures in the safety information. The serious-event term list is empty.

These safety counts should be read as descriptive observations, not as a powered comparison of safety between arms. Zero recorded serious events in both arms does not demonstrate equivalence, and the death counts alone do not establish causation. The registry record does not report a statistical analysis of adverse events.

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

The primary result describes a lower observed count proportion for antibiotic receipt or prescription in the rapid-testing arm than in usual care. The unadjusted risk-difference interval includes zero, and the p-value is 0.06. Together, these indicate uncertainty about the size and direction of the underlying difference. The posted data do not establish that the arms differed, but they also do not prove that they were the same.

The trial’s diagnostic secondary outcomes show more pathogen identification and laboratory-confirmed influenza in the rapid-testing arm. Those observations indicate a difference in recorded diagnostic findings in this study, not necessarily a difference in downstream treatment or patient health. The anti-influenza treatment comparison is uncertain, and the registry does not provide numerical results for several other listed secondary outcomes.

These results do not establish that rapid testing improves or worsens health, prevents unnecessary prescribing, changes hospital use, or affects mortality. The primary endpoint measures antibiotic receipt or a prescription, not whether the prescription was clinically appropriate or whether the patient took the medication. The registry does not provide enough outcome results or analysis details to answer broader questions about the full care pathway.

General statistical interpretation also distinguishes absence of clear evidence from evidence of absence. A confidence interval that includes zero can reflect an effect that is too imprecisely estimated to separate from no difference. The width and limits of the interval, study conduct, and analysis plan all matter. Because several design and analysis details are not reported in the registry record, conclusions should remain tied to the posted counts and their unadjusted comparisons.

17. Why This Trial Matters Statistically

This trial illustrates why diagnostic outcomes and treatment outcomes should be considered separately. Rapid testing can affect whether a pathogen is identified, while antibiotic prescribing is a distinct endpoint influenced by the clinical context and care decisions. In the posted results, the diagnostic outcomes have a clearer separation between arms than the primary prescribing outcome. That contrast is statistically informative without establishing a causal mechanism or a broader clinical benefit.

The primary endpoint also shows why an estimate should be interpreted together with its uncertainty. The observed direction alone might suggest a difference, but its interval includes zero and the unadjusted p-value is 0.06. Reading only the event counts, only the point estimate, or only a thresholded p-value would leave out important information. The interval conveys that the data are not precise enough to make a firm distinction.

The trial is also a useful example of how registry reporting shapes interpretation. Randomization and parallel-group design are reported, but the analysis plan, missing-data procedures, analysis populations, and multiplicity strategy are not. These omissions do not erase the descriptive results, but they limit assessment of how confirmatory the comparisons are and whether the reported calculations correspond to the intended analysis.

Finally, planning calculations based on an observed effect should not be mistaken for the trial’s original design justification or for observed power. Their role is to illustrate how sample requirements depend on the target effect and desired power under stated assumptions. That distinction matters when using a completed trial to inform future study planning.

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.

Several trial-specific limitations follow from the registry information available. The primary comparison is an unadjusted re-calculation from participant counts, and no formal reported analysis entry is listed. The record does not provide the original statistical analysis plan, so it is not possible to determine whether this comparison matches a prespecified method or whether other analyses were planned.

The usual-care arm could involve no test, point-of-care influenza testing, or delayed testing at an off-site laboratory. This makes the comparator clinically flexible, but the registry does not report how often each pathway was used. The intervention arm received rapid testing plus usual care, so the contrast is between a testing strategy and variable usual care, rather than rapid testing versus a single fixed diagnostic procedure.

The endpoint denominators vary. The primary outcome uses 93 and 98 participants, while the appropriate anti-influenza treatment outcome uses 93 and 37. The reasons for those denominators and their relation to eligibility, missing observations, or outcome-specific populations are not reported in the registry record. Total enrollment is listed as 194, without a reconciliation to the primary endpoint denominators.

The record does not state which party was masked, how allocation was implemented, how missing data were handled, or which analysis populations were used. It also does not report a multiplicity strategy, and numerical results for several listed secondary outcomes are not present in the available record. These limits constrain causal, safety, and generalizability claims; they do not justify assumptions about unreported trial procedures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Rapid Diagnostics for Upper Respiratory Infections in the Emergency Department — NCT02957136.
• Registry record last updated 2021-05-19; status last verified 2021-04.
• Results first posted 2021-02-02.
• 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

NCT02957136 is a completed randomized, parallel-group, single-masked trial sponsored by the University of California, Davis. It compared rapid respiratory pathogen nucleic acid amplification testing plus usual care with clinician-directed usual care in emergency department patients with influenza-like illness and/or upper respiratory symptoms. Enrollment is listed as 194.

The primary outcome was antibiotic receipt or an antibiotic prescription in the emergency department on Day 0. The posted counts were 20 of 93 in the rapid-testing arm and 33 of 98 in usual care. The unadjusted comparison is uncertain, with a p-value of 0.06 and an interval that includes zero. Secondary diagnostic outcomes show more pathogen identification and laboratory-confirmed influenza in the rapid-testing arm; other listed outcomes have incomplete numerical reporting. The analysis plan, missing-data methods, analysis populations, and original sample-size assumptions are not reported in the registry record.