The PATCH Trial (Prevention And Treatment of COVID-19 With Hydroxychloroquine): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The PATCH Trial (Prevention And Treatment of COVID-19 With Hydroxychloroquine) (NCT04329923), a randomized phase 2 study. The primary outcome is Time to Release From Quarantine Time.

2. Clinical Question

3. Trial Design

The PATCH Trial is registered as a randomized, parallel, phase 2 study of hydroxychloroquine for COVID-19 prevention and treatment. The registry classifies masking as triple. It describes three cohorts with different populations and treatment comparisons, so the overall enrollment of 173 should not be treated as the sample size for the primary Cohort 1 comparison.

Cohort 1 was a placebo-controlled comparison in home-quarantined COVID-19 PCR+ patients. The hydroxychloroquine regimen was 400 mg twice a day for up to 14 days; the placebo regimen was twice a day for up to 14 days. Crossover from placebo was allowed if symptoms worsened after 7 days. Cohort 2 enrolled hospitalized COVID-19 PCR+ patients and compared hydroxychloroquine 600 mg twice a day for up to 14 days with 600 mg once a day for up to 7 days. Cohort 3 was a placebo-controlled prevention cohort among health care workers at high risk of contracting COVID-19. Its hydroxychloroquine regimen was 600 mg once a day for 2 months, and crossover from placebo was allowed if a participant became SARS-CoV2 positive.

The registry lists Ravi Amaravadi, MD as sponsor and describes the trial as investigator-initiated. The study start date is 2020-04-09, the primary completion date is 2020-11-11, and the status is terminated. The reason for termination is not reported in the registry record. The registry does not report the original design assumptions or a rationale for the overall enrollment target.

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:

Analysis population for the primary outcome, as defined in the registry: randomized patients that were released from quarantine on study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All randomized patients

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Time to Release From Quarantine Time, measured over until quarantine release or hospitalization.

The primary endpoint is median time to release from quarantine, measured in days, for Cohort 1 home-quarantined COVID-19 patients. Release was defined using several conditions: no fever for 72 hours, improvement in other symptoms, and 7 or 10 days since the beginning of symptom onset, depending on CDC guidance at the time. The stated timeframe is until quarantine release or hospitalization.

A time-to-event endpoint is generally useful when the outcome involves both whether an event occurs and how long it takes to occur. In this trial, the event of interest is release from quarantine, and the median describes the middle of the observed time distribution. It differs from a simple average because it identifies the point by which half of the observed event times are at or below the median and half are at or above it.

The posted primary summaries give medians and full ranges. They describe time among randomized patients who were released from quarantine on study, rather than a summary that clearly includes every randomized patient. The registry does not report additional detail on how participants who were hospitalized, not released on study, or otherwise missing an observed release time were handled in this endpoint analysis.

7. Results Posted in the Registry

• Cohort 1 HCQ vs Cohort 1 Placebo: hazard ratio 0.58, reported p = 0.280 (as reported in the registry).

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.

Rate of Housemate Infection

• 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:
  • Cohort 1 HCQ: 11.8% (2/17) versus 11.8% (2/17) on control; risk difference 0.0 percentage points (95% CI -21.7 to 21.7), risk ratio 1.00 (0.16–6.30); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 1 HCQ and the control. The interval gives the range of effects that remain compatible with the data.

Rate of Hospitalization

• 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:
  • Cohort 1 HCQ: 5.9% (1/17) versus 0.0% (0/17) on control; risk difference 5.9 percentage points (95% CI -5.3 to 17.1); unadjusted two-proportion z-test p = 0.310.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 1 HCQ and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes give a mixed descriptive pattern rather than a clear, consistent account that resolves the primary result. Housemate infection had the same posted participant count in the two Cohort 1 groups, while hospitalization was recorded in the hydroxychloroquine group and not in the placebo group. The unadjusted risk-difference intervals for both outcomes include zero, and their p-values do not establish a definitive difference.

These outcomes relate to the primary endpoint but measure different things. Time to release from quarantine measures when a milestone occurred among the stated primary outcome population. Housemate infection concerns infection among household contacts, while hospitalization is a separate clinical event. Similarity or difference in these secondary summaries cannot validate or overturn the time-to-release result, and the measures may involve different analysis populations and follow-up details.

The registry does not list sponsor-reported analyses for the secondary outcomes. The posted risk-difference estimates and intervals are unadjusted re-calculations from group counts. Unadjusted secondary findings carry less weight as confirmatory evidence because evaluating multiple outcomes creates more opportunities for apparently notable patterns to arise by chance. The registry lists five outcome measures and one analysis, but it does not report whether multiplicity was addressed or how the outcomes were prioritized in the statistical plan.

The secondary outcomes are therefore best treated as exploratory context. Their uncertainty, the absence of reported sponsor analyses, and the lack of multiplicity information limit how strongly they can be used to support a claim about the treatment comparison. They do not supply the missing confidence interval for the primary hazard ratio.

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

• Rate of Housemate Infection
• Rate of Hospitalization

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical summaries address different features of the trial data. They should be read as complementary descriptions rather than interchangeable estimates.

What does the median summarize?

The primary outcome is a time-to-event measure: the recorded time from the relevant starting point to release from quarantine. The median is a location summary for those observed times. It is less influenced by unusually long values than an arithmetic mean, but a median alone does not describe the full distribution or quantify uncertainty about a group difference. The posted full ranges show the smallest and largest recorded values, not the precision of the median or an interval estimate for the treatment contrast.

There is an important population qualification. The primary outcome population is described as randomized patients who were released from quarantine on study. A time-to-event analysis can often include people who have not yet had the event by accounting for their follow-up up to a point of censoring. However, the registry does not explain whether or how censoring was used, how hospitalization was treated in the time-to-event model, or how participants without a recorded release were handled. Those details should not be inferred from the outcome title alone.

What does a Cox model estimate?

The reported method is Cox regression, and the reported parameter is a Cox proportional hazard ratio. In general, a hazard describes the instantaneous event rate among people still at risk at a given time, conditional on the model and its assumptions. A hazard ratio compares those modeled rates between groups. It is not a ratio of medians, and it is not a risk difference or a probability that an individual participant will experience the event.

The proportional hazards model generally assumes that the relative hazards are sufficiently stable over time for a single hazard ratio to be a useful summary. The registry does not report whether this assumption was assessed, which covariates were included, or the event coding used for the group contrast. The reported value of 0.58 therefore cannot be given a directional interpretation beyond identifying it as the posted hazard ratio for Cohort 1 hydroxychloroquine versus Cohort 1 placebo. The associated p-value is 0.28; no confidence interval is reported.

How should the secondary comparisons be read?

The secondary outcomes are counts of participants with housemate infection and hospitalization. A risk difference is an absolute contrast between the observed group proportions. General statistical interpretation treats a risk difference of zero as no observed difference in proportions, while a confidence interval describes uncertainty in the estimated contrast under the analysis method. The posted secondary comparisons are unadjusted re-calculations from the group summaries; the registry does not list sponsor-reported analyses for these outcomes.

For housemate infection, the posted risk difference is 0.0, with a confidence interval from -0.217 to 0.217 and an unadjusted p-value of 1.0. For hospitalization, the posted risk difference is 0.059, with a confidence interval from -0.053 to 0.171 and an unadjusted p-value of 0.31. Both intervals include zero. These summaries are based on small group counts, so the estimates are compatible with a wide range of possible group differences. They do not replace the primary time-to-event analysis, which addresses a different outcome.

What is the role of the reported p-value?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and its assumptions were true. It does not give the probability that the null hypothesis is true, and it does not measure clinical importance. The registry does not report the primary analysis significance threshold or a detailed statistical analysis plan, so a threshold should not be assumed when labeling the result. The planning illustration uses a two-sided significance level of 0.05, but that is a stated assumption for the illustration, not evidence of the trial’s original analysis plan.

Random allocation is recorded for the study, but the registry does not provide enough information to evaluate allocation implementation, baseline balance, adherence, or the effect of crossover. The design includes crossover permissions in Cohort 1 and Cohort 3. Crossover can complicate interpretation of a group comparison, depending on how participants are analyzed and how outcomes after crossover are handled. The registry does not report those analysis details.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated effect. A confidence interval gives a range of values compatible with the data and the method used, under the model’s assumptions. A narrow interval indicates greater precision than a wide interval, but it does not remove the need to consider bias, outcome definitions, or analysis choices.

The primary Cox hazard ratio is 0.58, and the reported p-value is 0.28. The registry does not report a confidence interval for the hazard ratio. As a result, the precision of that model-based estimate cannot be assessed from the posted primary comparison using an interval estimate. The medians of 8 days and 11 days and their full ranges of 4 to 19 days and 4 to 18 days describe the observed data, but they are not confidence intervals for a treatment effect.

The secondary comparisons do include intervals. For housemate infection, the risk-difference interval runs from -0.217 to 0.217. For hospitalization, it runs from -0.053 to 0.171. Each interval includes zero and covers values on either side of no difference, so these re-calculations do not tightly pin down the direction or size of the group contrast. The corresponding group counts are limited, which is consistent with substantial uncertainty, but the intervals are the direct summary of that uncertainty.

Precision should not be confused with whether a result is important. A precise estimate can still concern an outcome of limited relevance, and an imprecise estimate can leave a meaningful effect unresolved. Here, the primary estimate lacks a reported interval, while the secondary intervals are broad enough to encompass contrasting interpretations. The registry record does not report a fuller uncertainty analysis for the primary result.

12. Planning a Similar Trial: Sample Size

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

The planning values are illustrations based on the observed effect, not the trial’s original design. For the time-to-event endpoint, the figures are total events, not participants per arm. Under the stated scenario using 100% of the observed effect, the illustration lists 106 total events for 80% power and 142 total events for 90% power. At 75% of the observed effect, it lists 189 total events for 80% power and 252 total events for 90% power. At 50% of the observed effect, it lists 424 total events for 80% power and 567 total events for 90% power.

The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The 80% power column means the event target associated with an 80% chance of detecting the specified effect under those assumptions if that effect is real. The 90% power column expresses the corresponding target for a higher chance of detection. These are planning concepts, not guarantees about the results of any particular study.

Smaller effects require more information to distinguish them from chance variation. That is why the event targets rise as the planning effect moves from 100% to 75% to 50% of the observed effect. These figures are not participants per arm: they are total events for the Cox time-to-event calculation. The trial’s own original sample-size assumptions are not reported in the registry record. This is not observed power.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.580, so ln(HR) = -0.5447.
2. d = 4 × (1.96 + 0.842)² / [ln(0.580)]² = 105.8, rounded up to 106 events in total 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
hr <- 0.58                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(4329923)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 106 (80% power), 142 (90% power)
 75% of observed effect: events = 189 (80% power), 252 (90% power)
 50% of observed effect: events = 424 (80% power), 567 (90% power)
Simulated power with 106 events: 0.769 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 145 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 173 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 0.263013698630137          # control-arm median, months (converted from the posted unit)
hr          <- 0.58          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
       N: 52         p (1-sided)   0.0001
  Events: 48        ~HR at bound   0.3417
    Month: 9    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.58   0.0338
   IA 2: 67%                   Z   2.5114
      N: 100         p (1-sided)   0.0060
  Events: 96        ~HR at bound   0.5981
   Month: 17    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.58   0.5603
       Final                   Z   1.9930
      N: 146         p (1-sided)   0.0231
 Events: 144        ~HR at bound   0.7168
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.58   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The primary comparison uses the sponsor-reported Cox proportional hazards analysis: hazard ratio 0.58 and p = 0.28 for Cohort 1 hydroxychloroquine versus Cohort 1 placebo. No confidence interval is reported for that hazard ratio. Because this is a time-to-event result, it is not appropriate to replace the sponsor’s model estimate with a simple calculation from the posted medians. The registry does not provide the participant-level event times or model details needed to reproduce the Cox analysis.

The posted median and full-range summaries offer a descriptive view of the observed release times, but they are not a re-analysis of the Cox model. The secondary risk differences and their intervals are simple unadjusted re-calculations from posted group summaries; the registry lists no sponsor-reported analyses for those secondary outcomes. They answer different questions from the primary hazard ratio and should not be treated as competing estimates of the same endpoint.

The record does not flag a discrepancy between its reported primary analysis and the posted summaries. The sponsor analysis therefore remains the relevant reported model result for the primary endpoint. This does not make the result more precise than its reporting allows: the absent confidence interval and unreported model details remain important limitations.

16. Multiplicity, Missing Data and Analysis Populations

The registry record lists five outcome measures and one analysis. It does not report a detailed statistical analysis plan identifying which outcomes were confirmatory, the planned order of testing, or whether any multiplicity adjustment was used. Without that information, it is not possible to determine how the different outcomes were intended to contribute to the study’s formal conclusions.

Multiplicity matters because repeated testing across outcomes or subgroups increases the chance that at least one result appears notable by chance. General statistical practice may address this with a prespecified hierarchy or adjustment, but the registry does not report such an approach for this trial. The unadjusted secondary p-values should therefore be interpreted cautiously and should not be treated as if they were protected from multiple comparisons.

Missing-data handling is also not reported in the registry record. For the primary endpoint, the stated analysis population is randomized patients who were released from quarantine on study. The record does not explain how participants who were hospitalized, not released on study, withdrew, or lacked an observed outcome were handled. It does not describe imputation, censoring rules, or sensitivity analyses. The secondary outcomes have posted denominators, but the registry does not explain whether all randomized participants were included in each analysis or how missing observations were handled.

The registry does not specify whether the primary analysis followed an intention-to-treat principle, a per-protocol approach, or another analysis population. It also does not report an interim analysis plan, stopping boundaries, or a missing-data sensitivity analysis. These omissions prevent assessment of whether the reported analysis followed a prespecified plan and how robust the estimates are to incomplete follow-up or analysis choices. The reason for trial termination is not reported, so its relationship, if any, to the statistical results cannot be evaluated from the registry record.

17. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (5.9%).

The adverse-event record reports serious adverse events by cohort and treatment group. In Cohort 1, the serious-event count was 1 among 17 participants at risk in the hydroxychloroquine group and 0 among 17 participants at risk in the placebo group. The registry identifies hospitalization as the top serious event term, reported as 5.9%. In Cohort 2, serious-event counts were 0 in both the high-dose and low-dose groups; in Cohort 3, serious-event counts were 0 in both the hydroxychloroquine and placebo groups. The record lists 0 deaths for every group.

These counts describe events recorded in the registry, not comparative proof of safety or harm. The cohorts involve different populations, regimens, and follow-up contexts, so their adverse-event counts should not be pooled into a single interpretation. The registry does not provide additional detail about event timing, severity grading, attribution to treatment, or statistical comparisons. Low counts, including zero counts, do not establish that an event cannot occur.

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

The posted results describe a randomized, parallel, phase 2 trial with three distinct COVID-19 cohorts. The primary endpoint concerns time to release from quarantine in home-quarantined Cohort 1 patients. The hydroxychloroquine group’s posted median was 8 days and the placebo group’s was 11 days, with overlapping full ranges. The sponsor-reported Cox hazard ratio was 0.58, with p = 0.28 and no reported confidence interval. Taken together, these data do not give a precise estimate of the primary treatment contrast.

They do not establish that hydroxychloroquine caused a difference in time to release, and the hazard ratio’s direction cannot be translated into faster or slower release from the registry information alone because event coding is not described. Nor do the secondary housemate-infection and hospitalization summaries settle the primary question: their unadjusted intervals include zero, and the registry does not report sponsor analyses for them.

The overall enrollment of 173 includes the broader trial, while the primary endpoint summary refers to a narrower stated population. These figures should not be treated as interchangeable. The three cohorts also address different settings and regimens, so a result for home-quarantined patients does not automatically describe hospitalized patients or health care workers.

The record does not report the original sample-size rationale, missing-data methods, multiplicity strategy, full statistical plan, or reason for termination. Those gaps limit assessment of design intent and robustness. The findings are registry-reported statistical summaries, not medical advice and not a basis for an individual treatment decision. They should be understood within the endpoint definition, reported analysis population, and uncertainty limitations described in the registry record.

19. Why This Trial Matters Statistically

This trial illustrates why clinical results need to be read through the endpoint definition and analysis population, not only through a headline estimate. Time to release from quarantine is a time-to-event outcome, while housemate infection and hospitalization are participant-count outcomes. Each requires a different statistical summary, and none can be substituted for another without changing the question being answered.

It also shows why a median difference is not equivalent to a model-based treatment effect. The posted medians and full ranges are descriptive; the Cox hazard ratio is a separate summary whose interpretation depends on event coding and model assumptions. The registry reports a p-value but no confidence interval for the primary hazard ratio, leaving the precision of that estimate difficult to judge.

The planning illustration makes a further general point: detecting a smaller effect usually requires more events or participants, all else equal. Its event targets are based on the observed effect and stated planning assumptions, not the trial’s original design. That distinction matters because a retrospective planning illustration cannot tell readers whether the study was designed to answer its primary question with adequate precision.

Finally, the trial’s three cohorts make scope especially important. The same registry record describes home treatment, hospital dosing, and prevention among health care workers, but the posted primary result concerns only Cohort 1. Keeping population, treatment regimen, endpoint, and analysis aligned is essential for avoiding overgeneralization from a complex trial record.

20. 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 limitations are specific to this trial record. The primary endpoint is reported for randomized participants who were released from quarantine on study, which is narrower than an explicit all-randomized analysis population. The registry does not explain how hospitalization or participants without an observed release time were handled. Because the endpoint itself includes release or hospitalization in its timeframe, the absence of detailed event and censoring definitions complicates interpretation of the Cox analysis.

The quarantine-release criteria could use 7 or 10 days since symptom onset depending on CDC guidance at the time. This means the operational endpoint definition was not a single fixed interval in the record. The registry does not explain how the change was applied across participants or whether analyses accounted for it.

Crossover was allowed in Cohort 1 if symptoms worsened after 7 days of placebo treatment, and in Cohort 3 if a participant became SARS-CoV2 positive. The registry does not describe how crossover was incorporated into analysis. Cohort 2 used two hydroxychloroquine doses without a placebo arm, and the three cohorts had different populations and treatment schedules. Results therefore cannot be interpreted as one uniform comparison across the whole trial.

The primary hazard ratio has no reported confidence interval, and the statistical model’s event coding and covariate specification are not reported. The registry also lacks details on missing-data methods, multiplicity, original sample-size assumptions, and the reason for termination. Overall enrollment is reported as 173, but it is not the primary endpoint analysis size. These gaps limit assessment of precision, robustness, and generalizability.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: The PATCH Trial (Prevention And Treatment of COVID-19 With Hydroxychloroquine) — NCT04329923.
• Registry record last updated 2020-12-10; status last verified 2020-12.
• Results first posted 2020-12-10.
• 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.

24. Record Summary

The PATCH Trial is registered as a randomized, triple-masked, parallel phase 2 study of hydroxychloroquine for COVID-19, with three cohorts: home-quarantined patients, hospitalized patients, and health care workers at high risk. The registry reports overall enrollment of 173 and lists the status as terminated.

The primary outcome is median time to release from quarantine in Cohort 1. The posted medians are 8 days for hydroxychloroquine and 11 days for placebo. The sponsor-reported Cox hazard ratio is 0.58, with p = 0.28; a confidence interval is not reported. Secondary outcomes concern housemate infection and hospitalization, with unadjusted re-calculations whose intervals include zero.

The registry does not report the original design assumptions, a detailed analysis plan, missing-data methods, multiplicity handling, or the reason for termination. The primary results are best read as limited registry summaries with important uncertainty and analysis details unavailable.