Hormonal Intervention for the Treatment in Veterans With COVID-19 Requiring Hospitalization: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hormonal Intervention for the Treatment in Veterans With COVID-19 Requiring Hospitalization (NCT04397718), a randomized phase 2 study. The primary outcome is Composite of Mortality, Ongoing Need for Hospitalization, or Mechanical Ventilation at Day 15.

2. Clinical Question

The trial addressed whether temporary androgen suppression, using degarelix, was associated with clinical outcomes in hospitalized veterans with COVID-19. Its comparison was between two groups receiving BSC: one also received degarelix, while the other received placebo. The primary endpoint brought together three events that indicate a serious ongoing clinical course: death, continued need for hospitalization, and mechanical ventilation by Day 15.

This composite records whether a participant experienced at least one of its components by the specified time. It gives a summary across several possible outcomes, but does not by itself show which component accounts for a group difference. The registry record also lists secondary outcomes relating to clinical improvement, mortality, hospitalization, intubation, temperature, illness severity, and a day-30 composite. Results for individual secondary outcomes should be interpreted as additional evidence rather than as replacements for the primary comparison.

The clinical question is specific to the enrolled population and the recorded follow-up. The registry record does not establish whether the findings apply to people outside the hospitalized veteran population or to settings beyond the acute care ward.

3. Trial Design

HITCH was a multicenter, phase 2 randomized controlled trial with a parallel-group design and double masking. The registry lists an enrollment of 96. Participants were assigned to placebo plus BSC or degarelix plus BSC; the posted primary results include 34 participants in the placebo group and 62 in the degarelix group. These are the group sizes reported for the primary endpoint, not an assertion about the intended allocation ratio.

The active group received degarelix alongside best supportive care. The comparison group received saline placebo alongside best supportive care. Thus, the contrast concerns adding degarelix rather than comparing supportive care with no care. The registry identifies the sponsor as the VA Office of Research and Development and the status as completed. The recorded start date is 2020-07-06, and the primary completion date is 2021-06-08.

Randomization is intended to support a fair comparison by assigning participants to treatment groups through a chance-based process. Double masking is intended to reduce the influence of treatment knowledge on participants’ experiences and on aspects of study conduct or outcome assessment. The registry record does not report details of how masking was maintained or assessed, the randomization procedure, or the allocation sequence.

The phase 2 designation describes the trial’s stage in clinical development; it does not, on its own, determine whether an estimate is precise or whether a result is conclusive. The registry record does not report the original sample-size justification or the detailed design assumptions used for the trial. The planning illustrations based on observed effects are separate from those original design assumptions.

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 Composite of Mortality, Ongoing Need for Hospitalization, or Mechanical Ventilation at Day 15, measured over 15 days.

The primary endpoint counts participants who had died, remained in need of hospitalization, or had been placed on mechanical ventilation at Day 15. It is a binary composite: a participant is counted if the recorded outcome meets the composite definition, rather than being assigned a separate score for each component. The posted counts are 9 of 34 participants in the placebo plus BSC group and 19 of 62 in the degarelix plus BSC group.

A composite endpoint can represent several clinically serious ways in which a participant may continue to experience a poor course. Combining components can make a single summary relevant to different pathways through illness. That summary has a trade-off: it does not distinguish the components or indicate whether a group contrast is driven by death, ongoing hospitalization, or mechanical ventilation. The component-specific counts for this day-15 composite are not reported in the registry record.

The registry describes the endpoint as the number of participants with the composite outcome at Day 15. The choice of a fixed assessment time makes the outcome a comparison of status by that time, rather than a measure of how quickly each component occurred. The registry record does not report additional detail about how the status of participants with incomplete day-15 follow-up was handled.

7. Results Posted in the Registry

• Degarelix + BSC: 30.6% (19/62) versus 26.5% (9/34) on control; risk difference 4.2 percentage points (95% CI -14.6 to 22.9), risk ratio 1.16 (0.59–2.27); unadjusted two-proportion z-test p = 0.667.

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.

Time to Clinical Improvement

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Placebo + BSC vs Degarelix + BSC: hazard ratio 0.93 (95% CI 0.58–1.49), reported p = 0.876 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo + BSC vs Degarelix + BSC and the control. The interval gives the range of effects that remain compatible with the data.

Inpatient Mortality

• 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:
  • Degarelix + BSC: 17.7% (11/62) versus 17.6% (6/34) on control; risk difference 0.1 percentage points (95% CI -15.9 to 16.1), risk ratio 1.01 (0.41–2.48); unadjusted two-proportion z-test p = 0.991.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Degarelix + BSC and the control. The interval gives the range of effects that remain compatible with the data.

Time to Normalization of Temperature.

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Placebo + BSC vs Degarelix + BSC: hazard ratio 2.30 (95% CI 0.72–7.39), reported p = 0.100 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo + BSC vs Degarelix + BSC and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering clinical improvement, inpatient mortality, hospitalization, intubation, temperature normalization, illness severity, and a day-30 composite. The detailed results include time-to-event comparisons and participant counts for some of these outcomes. Across the reported secondary measures, the estimates do not form a uniformly precise pattern pointing in one direction. Their uncertainty and the different outcome scales matter when considering whether they reinforce or qualify the primary finding.

Secondary outcomes can add context by examining different aspects of the clinical course. They do not change what the primary endpoint measures, and variation across endpoints is not by itself evidence that one result is correct and another is not. Some outcomes concern the timing of an event, while others count participants with an event; results on these different scales cannot be read as direct repetitions of the primary comparison.

Multiple secondary comparisons create more opportunities for apparently notable findings to occur by chance. Unless a suitable multiplicity strategy is prespecified and applied, individual secondary p-values generally carry less confirmatory weight than a single primary comparison. Whether an adjustment or a hierarchy for interpreting secondary outcomes was planned is not reported in the registry record. The secondary findings are therefore best viewed as exploratory context rather than as independent confirmation of a definitive treatment effect.

The registry record does not include detailed results for every listed secondary outcome in the information summarized for this trial. For outcomes without a posted result, the result is not reported in the registry record. Absence of a reported estimate should not be interpreted as a favorable, unfavorable, or null finding.

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

• Time to Clinical Improvement
• Inpatient Mortality
• Duration of Hospitalization
• Duration of Intubation
• Time to Normalization of Temperature.
• Maximum Severity of COVID19 Illness.
• Composite of Mortality, Ongoing Need for Hospitalization, or Mechanical Ventilation at Day 30

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant met the composite definition by Day 15. For a binary outcome, a risk is the proportion of participants in a group who experienced the event. A risk difference compares those proportions by subtraction; a value of zero corresponds to equal observed risks, while values on opposite sides of zero indicate opposite directions of contrast. The posted recalculation estimates a risk difference of 0.042. Its 95% confidence interval, from -0.146 to 0.229, includes zero, so the data do not narrowly pinpoint a direction.

What does a confidence interval communicate?

In general, a confidence interval describes uncertainty around an estimate under the method’s assumptions. It is not a range that guarantees the true value lies within its endpoints, and it does not assign a probability to each possible effect. A wide interval indicates that the estimate is compatible with a broad range of values. For the primary outcome, the interval includes both negative and positive risk differences, so it does not resolve whether the population contrast favors one group or the other.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The reported primary p-value is 0.667. That value is not evidence of a clear departure from the null under the reported test, but it cannot establish equality or rule out effects that the confidence interval still allows.

Why are odds ratios different from risk differences?

An odds ratio compares the odds of an event between groups, whereas a risk difference compares event probabilities directly. They describe the same binary outcome on different scales. An odds ratio of 1 corresponds to equal odds; a risk difference of zero corresponds to equal risks. For uncommon outcomes, the two measures can sometimes be numerically similar, but they are not identical measures and should not be substituted for one another. The registry reports an odds ratio of 1.19 with a 95% confidence interval from 0.46 to 3.06. The recalculated comparison is a risk difference, so the estimates should be interpreted according to their respective scales.

What does the time-to-event method estimate?

For time-to-event outcomes, the registry reports log-rank comparisons and hazard ratios. In general, a hazard ratio compares event rates over follow-up among participants who have not yet experienced the event. It is not a difference in median days and does not directly state the probability of an event by a particular day. Interpretation depends on the event definition, follow-up, and analysis assumptions. The registry record does not report all details needed to assess those assumptions, including how censoring was handled.

The secondary temperature and clinical-improvement outcomes are presented as medians with interquartile ranges, alongside reported time-to-event comparisons. A median marks the midpoint of the observed distribution; an interquartile range describes the middle half of that distribution. These summaries answer different questions from a hazard ratio. They should not be treated as if they were interchangeable estimates of the same quantity.

Why can over-dispersion matter?

In general, over-dispersion means that observed variation is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if the analysis assumes less variation than the data contain. This concern is especially relevant when count outcomes are analyzed with models that impose a particular variance structure. The primary endpoint is reported as a count of participants with a binary event, and dispersion is not reported as a separate endpoint quantity. The registry record does not provide enough information to infer that over-dispersion was assessed or to identify a model adjustment for it.

All statistical explanations in this discussion describe general concepts; the registry record does not report a complete statistical analysis plan. In particular, the record does not report all model details, the prespecified handling of missing observations, or the analysis population definition. These omissions limit how fully a reader can evaluate the assumptions behind the reported estimates.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the available data. For the primary risk difference, the estimate is 0.042, while its 95% confidence interval extends from -0.146 to 0.229. The interval covers zero and also allows contrasts in either direction. This breadth means the observed estimate should not be read as a precise measure of the underlying difference.

The sponsor-reported odds ratio is 1.19, with a 95% confidence interval from 0.46 to 3.06. That interval also includes the value corresponding to no difference in odds and allows a broad range of contrasts. Because the odds ratio and risk difference use different scales, the two intervals answer related but distinct questions.

A confidence interval is informative beyond whether it includes a null value. It shows which effect sizes remain compatible with the data under the stated method. A result that does not meet a conventional threshold for statistical evidence can still be too imprecise to rule out meaningful differences in either direction. Conversely, the point estimate alone should not be treated as a stable estimate when uncertainty is broad.

The primary group sizes were 34 and 62, and the observed counts were 9 and 19. Those data yield the reported level of uncertainty; the confidence interval does not remove uncertainty about unmeasured or unreported aspects of trial conduct. The registry record does not report further details such as missing-data handling that could help assess sensitivity of the estimate to those choices.

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 illustrations translate the observed effect into hypothetical sample-size requirements; they are not the trial’s original design justification. For binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events, not participants per arm. These quantities answer different planning questions and should be read according to the outcome type.

The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is defined as a stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes a hypothetical design that would have an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one and the assumptions held. The 90% power column describes the corresponding design with a 90% chance. These are design probabilities, not probabilities that the treatment effect is real.

For the primary composite, the illustration for 100% of the observed effect lists 1,837 participants per arm for 80% power and 2,459 participants per arm for 90% power. For 75% of the observed effect, it lists 3,230 and 4,324 participants per arm; for 50% of the observed effect, it lists 7,185 and 9,618 participants per arm. Smaller effects require more participants because they are harder to distinguish from random variation under the same assumptions. These figures are 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

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 = 0.265; treatment proportion p₁ = 0.306; average p̄ = 0.286.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6388 = 1.2520.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6381 = 0.5370.
4. n = (1.2520 + 0.5370)² / (0.0417)² = 1,836.6, rounded up to 1,837 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 <- 0.264705882352941                          # control proportion
p1 <- 0.306451612903226                          # 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(4397718)
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 = 1,837 (80% power), 2,459 (90% power)
 75% of observed effect: n per arm = 3,230 (80% power), 4,324 (90% power)
 50% of observed effect: n per arm = 7,185 (80% power), 9,618 (90% power)
power.prop.test: 1836.6 
Simulated power at n = 1,837 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a chi-squared comparison of odds, with an odds ratio of 1.19, a 95% confidence interval from 0.46 to 3.06, and p = 0.667. The unadjusted recalculation from the posted group summaries expresses the contrast as a risk difference of 0.042, with a 95% confidence interval from -0.146 to 0.229. Because these estimates use different effect scales, their numerical values should not be compared as though they were estimates of the same quantity.

The p-value reported by the sponsor is 0.667, matching the p-value in the unadjusted recalculation. The registry record does not identify a discrepancy between the sponsor’s analysis and the recalculation. The sponsor-reported result is the trial’s own analysis; the recalculation is a simple, unadjusted way to express the posted summary data and does not replace the reported analysis.

Both presentations indicate substantial uncertainty: the reported odds-ratio interval includes the null value for that measure, and the recalculated risk-difference interval includes zero. Neither the point estimate nor the p-value alone determines the size or certainty of the treatment contrast. The reported analysis should be read with its confidence interval and with the limits of the available registry information.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons, or analyses. As the number of statistical tests increases, the chance of at least one apparently unusual result arising by chance can also increase. One way to address this is to prespecify which outcome is primary and to define an adjustment or ordered testing procedure for additional outcomes. Whether the trial used such a procedure is not reported in the registry record.

The record identifies a primary endpoint and lists secondary outcomes, which helps distinguish the main question from additional questions. However, the detailed multiplicity strategy, any hierarchy among secondary outcomes, and any adjustment to secondary p-values are not reported in the registry record. Secondary results should therefore not be treated as if each were a separately confirmed primary finding.

Missing-data methods can also affect interpretation. The registry record does not report how missing endpoint observations were handled, whether any imputation was used, or what assumptions were made about participants without a recorded outcome. The record does not report a complete analysis population definition, such as the exact rule used to include participants in each analysis. Those details are relevant because exclusions or unobserved outcomes can affect group comparisons.

The registry reports eight outcome measures and eight analyses, but the presence of an analysis count does not by itself document the full statistical plan. The original sample-size justification, interim-analysis procedures, and detailed analysis plan are not reported in the registry record. These items should not be inferred from the posted outcome estimates or the separate planning illustrations.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 pneumonia (11.8%), respiratory failure (11.8%), septic shock (6.5%), covid-19 (4.8%), renal failure (3.2%).

The adverse-event record lists serious adverse events affecting 11 of 34 participants in the placebo plus BSC group and 19 of 62 participants in the degarelix plus BSC group. It lists other adverse events affecting 8 of 34 and 13 of 62 participants, respectively. Deaths are separately listed as 7 and 11 in the two groups. These are registry counts and should be read with their group denominators; they are not, by themselves, adjusted comparisons.

Serious-event terms listed in the registry include COVID-19 pneumonia and respiratory failure, each shown as 11.8%, followed by septic shock at 6.5%, COVID-19 at 4.8%, renal failure at 3.2%, and gastroenteritis at 2.9%. The registry’s displayed term percentages should be interpreted as recorded; the record does not provide enough detail to reconstruct their denominators or determine whether terms overlap within participants.

Adverse-event counts do not establish that an event was caused by a study intervention. The registry record does not report a detailed attribution analysis or enough context to assess differences in event severity, timing, or exposure. The adverse-event listings are descriptive safety information, not a basis for individual treatment decisions.

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

The primary data show the number of participants meeting a serious day-15 composite in each randomized group, together with an estimated contrast and its uncertainty. The interval around the recalculated risk difference includes zero and allows differences in either direction. The sponsor-reported odds-ratio interval likewise spans its null value. These results do not precisely establish the direction or size of the underlying contrast.

A result that is not statistically persuasive is not equivalent to proof of no effect. The trial’s data leave uncertainty about what contrasts may be compatible with the outcome, and the broad intervals make it inappropriate to present the point estimate as a precise answer. Equally, the observed counts should not be interpreted as evidence that one intervention caused an outcome difference.

The result is specific to a phase 2 randomized comparison among veterans hospitalized with COVID-19 on an acute care ward, using the recorded supportive-care and placebo or degarelix regimens. It concerns the composite outcome at Day 15. It does not, by itself, answer questions about each composite component separately, outcomes beyond the recorded follow-up, other patient populations, or other care settings.

The registry also reports secondary outcomes and adverse-event counts, but their differing definitions and levels of uncertainty should be kept in view. The posted findings can inform understanding of this trial’s estimates; they do not establish a general treatment conclusion. The registry record does not report enough detail about missing data, analysis populations, or the original statistical plan to resolve every methodological question.

18. Why This Trial Matters Statistically

This trial illustrates why effect estimates need to be read together with their uncertainty. The primary result has a point estimate, a confidence interval spanning both directions, and a p-value that does not indicate a clear departure from the null under the reported test. Treating only the point estimate or only the p-value as the conclusion would leave out important information about precision.

It also illustrates the distinction between an absolute measure and a relative measure. The recalculation reports a risk difference, while the registry’s analysis reports an odds ratio. Each communicates a group contrast on a different scale. Clear interpretation requires naming the scale and avoiding direct numerical comparisons between unlike measures.

The composite endpoint makes a single summary from several serious outcomes, but that summary can conceal which components contributed to the result. The listed secondary outcomes extend the picture of clinical course, yet multiple comparisons and heterogeneous outcome types make it important to avoid treating every result as confirmatory.

Finally, the trial’s planning illustrations are not evidence of the trial’s observed power or of its original design rationale. They show how required sample sizes change when the effect targeted for detection changes under stated assumptions. Distinguishing that planning exercise from the trial’s actual design assumptions helps prevent retrospective calculations from being mistaken for prespecified justification.

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.

The primary result comes from 96 enrolled participants, with posted primary endpoint groups of 34 and 62. Those group sizes and the observed event counts are associated with broad uncertainty in the estimated contrast. The trial was phase 2, and the registry record does not report the original sample-size justification or the assumptions used to plan the trial.

The primary endpoint combines death, ongoing hospitalization, and mechanical ventilation at Day 15. The registry record does not report component-specific counts for this composite, so the overall result cannot show which component contributed most. It also provides a fixed-time composite rather than a full account of the timing and course of each component.

The population was hospitalized veterans with COVID-19 on an acute care ward. The registry record does not establish whether the estimates apply to other populations or care settings. The record does not report full details of the randomization process, masking procedures, analysis populations, or handling of missing outcome data. These omissions limit assessment of design and analysis choices.

Several secondary outcomes are listed, but results for outcomes such as duration of hospitalization, duration of intubation, maximum illness severity, and the day-30 composite are not reported in the registry record. The multiplicity strategy and any adjustment of secondary comparisons are also not reported in the registry record. These limitations counsel against overinterpreting isolated secondary findings or treating unreported outcomes as evidence of no difference.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Hormonal Intervention for the Treatment in Veterans With COVID-19 Requiring Hospitalization — NCT04397718.
• Registry record last updated 2022-06-06; status last verified 2022-06.
• Results first posted 2022-06-06.
• 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

HITCH was a completed, multicenter, phase 2, randomized, double-masked, parallel-group trial in hospitalized veterans with COVID-19. It compared placebo plus best supportive care with degarelix plus best supportive care. The registry lists 96 enrolled participants and identifies the VA Office of Research and Development as sponsor.

The primary endpoint counted participants who died, remained hospitalized, or were placed on mechanical ventilation by Day 15. The posted counts were 9 of 34 in the placebo group and 19 of 62 in the degarelix group. The recalculated risk difference was 0.042, with a 95% confidence interval from -0.146 to 0.229 and p = 0.667. The sponsor-reported odds ratio was 1.19, with a 95% confidence interval from 0.46 to 3.06 and p = 0.667.

The primary estimate is uncertain and does not precisely establish the direction or size of the group contrast. The registry record does not report the original sample-size justification, detailed multiplicity approach, missing-data handling, or complete analysis-population definitions.