Initiation of Hydrocortisone for the Treatment of Septic Shock: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Initiation of Hydrocortisone for the Treatment of Septic Shock (NCT02580240), a randomized na study. The primary outcome is 28-day Mortality.

2. Clinical Question

This is a question about a defined outcome and follow-up time, not a general comparison of every possible effect of hydrocortisone. Mortality is a binary endpoint: each participant either died within the stated period or did not. That makes the result relatively direct to interpret, although it does not describe when a death occurred within the period, the course of illness, or other outcomes that may matter to participants.

3. Trial Design

The registry identifies this as a randomized, parallel-group trial with quadruple masking. Participants were allocated to hydrocortisone or saline placebo. The record describes the placebo vials as identical to those containing hydrocortisone and says that placebo administration procedures were similar. It does not specify the identities of all groups covered by the term quadruple masking.

Enrollment was 118. The posted primary outcome counts are 19 deaths among 60 participants in the placebo group and 23 among 58 in the hydrocortisone group. The registry status is completed. The recorded study start was 2015-09, and primary completion was 2016-09. The sponsor was Northern Jiangsu People's Hospital. The phase is listed as NA.

The hydrocortisone regimen was described as a continuous infusion of 200 mg/d for 6d, followed by a taper. The taper began after all vasopressors had been discontinued; the record describes a half dose for three days, followed by a quarter dose for three days, and then stopping. The placebo description says its administration procedures were similar. The record does not provide further information about treatment adherence, protocol deviations, concomitant care, or the operational details of randomization.

Random allocation is intended to make treatment groups comparable on average, while masking is intended to reduce the influence of expectations on care and outcome assessment. These are general design principles, not evidence that every source of bias was eliminated in this trial. The registry record does not report the method used to generate the allocation sequence or conceal it, or which specific roles were masked. Those details 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 28-day Mortality, measured over 28 days.

The primary endpoint was 28-day mortality, defined as death from any cause at 28 days after the onset of septic shock. The posted results count participants who experienced that event: 19 in the placebo group and 23 in the hydrocortisone group. The corresponding group sizes are 60 and 58, respectively.

All-cause mortality is a binary endpoint. It records whether the event occurred by the specified time, without distinguishing causes of death. Using a fixed follow-up point makes the comparison easier to state and avoids requiring a model of the timing of events. This is a general advantage of a binary outcome; it does not mean that information about the timing or circumstances of death is unimportant.

The endpoint is clinically consequential and unambiguous in concept, but its interpretation depends on complete and comparable outcome ascertainment. The registry record does not describe how vital status was collected, how deaths were verified, or how participants with unknown status were handled. Those procedures are not reported in the registry record. Nor does the primary endpoint alone describe other aspects of septic shock, treatment burden, or adverse effects. It answers the posted mortality question at the stated follow-up time, rather than providing a complete account of the trial’s outcomes.

7. Results Posted in the Registry

• Hydrocortisone: 39.7% (23/58) versus 31.7% (19/60) on control; risk difference 8.0 percentage points (95% CI -9.2 to 25.2), risk ratio 1.25 (0.77–2.04); unadjusted two-proportion z-test p = 0.365.

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.

All Cause 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:
  • Hydrocortisone: 39.7% (23/58) versus 31.7% (19/60) on control; risk difference 8.0 percentage points (95% CI -9.2 to 25.2), risk ratio 1.25 (0.77–2.04); unadjusted two-proportion z-test p = 0.365.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hydrocortisone and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: all-cause mortality at 90 days. Its posted counts are 19 of 60 in the placebo group and 23 of 58 in the hydrocortisone group, the same counts listed for the 28-day primary endpoint. The registry record does not explain the repeated values, provide a separate reported analysis, or describe whether there were changes in vital status after the primary follow-up point.

In broad direction, the secondary entry has the same displayed group pattern as the primary entry. It therefore does not present a contrasting set of posted counts. That similarity should be interpreted cautiously: identical counts in the registry do not establish that the outcome was analyzed independently, that no deaths occurred between follow-up times, or that the underlying data were checked for consistency. Those details are not reported in the registry record.

Secondary outcomes generally help explore whether the primary finding is accompanied by a consistent pattern in other measures or time periods. They do not automatically have the same evidential status as the primary outcome. If many outcomes or analyses are examined, the chance of finding apparently notable results by chance can increase. Adjustments for multiple comparisons, or a clearly prespecified hierarchy of outcomes, can address some of that concern. The registry record does not report a multiplicity strategy or a statistical analysis plan.

Here, there is no reported secondary analysis to add inferential weight to the primary comparison. The 90-day entry should be treated as a posted outcome record with its own stated time frame, not as independent confirmation of the 28-day result. The primary endpoint remains the main basis for the trial’s posted treatment comparison, while the secondary information is limited by the lack of analysis details and the repeated counts.

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

• All Cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

A risk difference compares the event risk in one group with the event risk in another. For this binary endpoint, the event is death by the stated follow-up time. A positive difference in the posted comparison means the estimated event risk is higher in the hydrocortisone group than in the placebo group; a negative difference would indicate the reverse. A value of zero represents no difference in estimated risk. This is a general explanation of the measure.

The registry reports group event counts, group sizes, a risk-difference estimate, its confidence interval, and an unadjusted p-value. The risk difference is an absolute measure: it expresses the gap in event probability between the groups, rather than how many times larger one risk is than the other. The reported estimate is positive. Its confidence interval crosses zero, so the data are compatible with a range that includes no absolute difference and possible differences in either direction.

How should a confidence interval be understood?

A confidence interval represents uncertainty around an estimate under the statistical method used. In general, an interval that includes the no-difference value indicates that the data do not rule out no difference at the corresponding confidence level. It does not mean that every value in the interval is equally likely, and it is not a range guaranteed to contain the true effect. Repeated use of the same method under its assumptions would produce intervals with the stated coverage in the long run. These are general properties of confidence intervals.

The interval’s width is relevant as well as whether it crosses zero. A wide interval signals limited precision: several materially different effects remain compatible with the observed data. Here, the reported risk-difference interval extends to both sides of zero. The record does not supply a clinical threshold for deciding which differences would be important, so statistical compatibility alone cannot identify what would be clinically meaningful.

What does the unadjusted p-value test?

The unadjusted p-value of 0.365 is a measure of how compatible the data are with a specified no-difference model, given the test’s assumptions. It is not an effect size, and it does not describe the chance that treatment is beneficial or harmful. “Unadjusted” means that the reported result is not presented as adjusted for other variables. The registry record does not report a model specification, covariate adjustment, or further details of the test used, so those details should not be inferred.

A p-value is not a substitute for the effect estimate and its uncertainty. A result can have a p-value that does not meet a conventional significance threshold while still allowing effects that may matter; conversely, a small p-value would not by itself show that an effect is large or important. In this trial, the direction of the point estimate, the interval spanning zero, the event counts, and the p-value all contribute to interpretation. None should be treated as a complete summary on its own.

How do risk ratios and odds ratios differ?

Risk ratios compare the event risk in one group with the event risk in another as a ratio. Odds ratios compare the odds of an event rather than the event risks themselves. Both are relative measures, whereas a risk difference is an absolute measure. Their numerical interpretation is therefore different. The registry reports a risk ratio of 1.252 and an odds ratio of 1.418 for the hydrocortisone comparison. As with the risk-difference estimate, these are estimates from the posted data, not guarantees of the underlying effect.

Relative measures can be useful for describing how groups compare proportionally, but they do not replace the underlying counts or an absolute measure. The same relative measure can correspond to different absolute differences in settings with different baseline risks. In this record, the placebo group’s posted event count and denominator provide context for the absolute risk comparison. The registry does not state a preferred measure or a clinical threshold for interpreting these estimates.

What information is absent about the analysis?

The registry lists no reported analyses. It does post an unadjusted comparison, but does not report details about the statistical test, handling of missing outcome data, analysis population, or treatment of protocol deviations. These omissions limit assessment of how closely the posted estimates follow a prespecified plan. The registry record does not report the trial’s original statistical analysis plan or its original design assumptions.

General statistical interpretation also depends on the quality and completeness of the data. Randomization supports a fair comparison when participants are analyzed appropriately and outcomes are ascertained comparably. Masking can reduce some sources of differential assessment, but it does not by itself establish complete follow-up or eliminate all bias. The registry record does not provide enough detail to assess those aspects. Accordingly, the numerical results can be described and their uncertainty discussed, while conclusions about the full conduct and analysis of the trial remain limited.

11. Confidence Intervals and Precision

The primary risk-difference estimate is accompanied by a confidence interval whose lower endpoint is negative and whose upper endpoint is positive. Because zero lies between those endpoints, the interval includes no difference. It also includes values corresponding to a higher risk in either group. This is the central precision message: the posted estimate has a direction, but the uncertainty does not tightly determine the direction or magnitude of the underlying difference.

A confidence interval is not a statement that the true effect has a particular probability of lying within the observed bounds. It describes the performance of an interval-producing method over repeated studies under its assumptions. In practical reading, the interval helps show which effects remain compatible with the data. Here it permits more than one interpretation, including no difference. The registry does not report a threshold separating clinically important from unimportant effects, so the interval cannot be classified solely by statistical criteria as clinically acceptable or unacceptable.

The p-value of 0.365 is consistent with that uncertainty, but the p-value and interval answer different descriptive questions. The p-value summarizes compatibility with a no-difference model; the interval communicates uncertainty across a range of effect values. Neither turns the observed comparison into proof of equivalence, nor does either show that a difference exists.

The event counts and group sizes are important context for precision. Mortality was observed in 19 participants in the placebo group and 23 in the hydrocortisone group, with group sizes of 60 and 58. The information available for estimating a difference is therefore limited, and a modest change in observed events could influence the estimate. This is a general consideration for binary outcomes, not a claim that the posted outcomes are unreliable. The registry record does not report a prespecified equivalence margin or a precision target against which the interval could be judged.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, rather than the trial’s original sample-size calculation. The assumptions listed for these calculations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

For planning for 100% of the observed effect, the figures are 564 participants per arm for 80% power and 754 participants per arm for 90% power. For planning for 75% of the observed effect, they are 990 participants per arm for 80% power and 1,324 participants per arm for 90% power. For planning for 50% of the observed effect, they are 2,197 participants per arm for 80% power and 2,940 participants per arm for 90% power.

In general, 80% power means that a study designed under the stated assumptions would have an 80% chance of detecting the specified effect at the chosen significance level if that effect were the true effect and the assumptions held. The 90% column describes the corresponding design with a higher chance of detecting that specified effect. Power is tied to a particular effect and analysis; it is not a guarantee that a study will produce a statistically significant result.

Smaller effects require more participants to detect with the same power and significance level. The pattern in these planning figures reflects that principle. These are not observed power calculations; they are planning illustrations based on the effect estimated in this trial. The registry record does not report the trial’s own original sample-size assumptions or justification.

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 = 0.317; treatment proportion p₁ = 0.397; average p̄ = 0.357.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6774 = 1.3277.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6750 = 0.5681.
4. n = (1.3277 + 0.5681)² / (0.0799)² = 563.2, rounded up to 564 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 <- 0.316666666666667                          # control proportion
p1 <- 0.396551724137931                          # 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(2580240)
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 = 564 (80% power), 754 (90% power)
 75% of observed effect: n per arm = 990 (80% power), 1,324 (90% power)
 50% of observed effect: n per arm = 2,197 (80% power), 2,940 (90% power)
power.prop.test: 563.2 
Simulated power at n = 564 per arm: 0.800 (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

Multiplicity arises when a study evaluates multiple outcomes, time points, treatment comparisons, or analyses. Each additional test creates another opportunity for a result to appear notable by chance, even when there is no true effect. This is a general statistical issue. Prespecified outcome hierarchies or multiplicity adjustments can help control the interpretation of a family of tests, but they require an analysis plan that defines the relevant tests and approach.

The registry lists 2 outcome measures and one posted secondary outcome, but it does not report a multiplicity procedure or explain how the primary and secondary outcomes were prioritized analytically. It records no reported analyses. The unadjusted p-value for the primary comparison should therefore be understood as an unadjusted result, not as a value known to account for all possible outcomes or analyses. It is not possible to determine from the registry whether other analyses were planned or performed outside the posted record.

Missing-data handling is also not reported in the registry record. The primary counts have denominators of 60 for placebo and 58 for hydrocortisone, but the record does not explain whether all randomized participants had an outcome recorded, how unknown vital status was treated, or whether any imputation or sensitivity analysis was used. The counts alone cannot answer those questions. Missing outcome information can affect a comparison if it differs between groups or is related to the outcome; this is a general concern, not a claim that missing data occurred in this trial.

The analysis population is not reported. The registry does not say whether results were analyzed according to randomized assignment, treatment received, or another population definition. It also does not describe deviations from the assigned intervention or how such deviations were handled. These details matter because exclusions or reassignment after randomization can weaken the comparability created by random allocation.

Without a reported analysis plan, multiplicity approach, missing-data procedure, and population definition, the posted estimates remain interpretable as registry results but cannot be fully assessed against the intended analysis. These omissions do not establish that the analyses were inappropriate; they limit what can be concluded about their prespecification and robustness.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hyperglycemia (1.7%).

The adverse-event record lists serious adverse events affecting 0 of 60 participants in the placebo group and 1 of 58 in the hydrocortisone group. For other adverse events, it lists 2 of 60 in the placebo group and 1 of 58 in the hydrocortisone group. The most frequent serious adverse-event term listed is hyperglycemia, at 1.7%.

These are small event counts, and they should be read as the registry’s reported counts rather than as a complete estimate of comparative safety. A count of zero in the posted serious-event category does not prove that no serious harm is possible. Likewise, one or two reported events cannot precisely establish whether the groups differ in risk. The record does not provide definitions of serious and other adverse events, event-level descriptions, severity grading, relatedness assessments, or a fuller account of how events were collected.

The death counts are also posted as the primary mortality outcome, but the registry does not describe how deaths relate to its adverse-event categories. They should not be added to adverse-event counts or treated as separate events without further information. The safety entries offer a limited description of reported events; they do not support a broad safety conclusion on their own.

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

The posted primary results describe a randomized comparison of hydrocortisone and saline placebo for 28-day mortality after septic shock onset. Deaths were recorded for 19 participants in the placebo group and 23 in the hydrocortisone group. The risk-difference estimate points toward higher mortality in the hydrocortisone group, while its confidence interval includes zero and the unadjusted p-value is 0.365. Together, these results show an uncertain comparison, not a precise determination of the treatment effect.

The findings do not establish that hydrocortisone increases mortality, because the interval includes no difference and possible effects in the opposite direction. They also do not establish that the groups are equivalent: no equivalence margin is reported, and the interval does not confine the estimate to a defined range of negligible effects. A non-significant p-value is not proof that two treatments have the same effect.

The registry’s stated interest in the timing of low-dose hydrocortisone should be distinguished from the posted treatment comparison. The registry reports a hydrocortisone regimen and a placebo arm, but does not report a separate randomized comparison of different initiation times or a timing-specific analysis. The results therefore cannot answer the timing question independently.

The secondary 90-day mortality entry repeats the primary outcome counts, and no separate secondary analysis is reported. That entry does not provide independent confirmation or additional information about deaths after day 28. Adverse-event counts are also sparse and lack important descriptive details, so they cannot settle the broader safety profile.

Overall, the registry record documents a completed randomized trial and posts an estimate with substantial uncertainty. It supports a description of what was observed in the recorded groups, but it does not support a definitive causal conclusion about benefit or harm. Missing information about outcome ascertainment, analysis populations, missing data, and the original analysis plan further limits assessment of robustness.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized design and an interpretable endpoint do not automatically produce a decisive estimate. Random allocation and quadruple masking are features intended to strengthen a comparison, and all-cause mortality at a fixed follow-up point is a direct binary outcome. Yet the posted counts still yield an imprecise estimated difference, with a confidence interval that includes no difference and effects in either direction.

It also demonstrates the value of considering absolute and relative measures alongside event counts. A risk difference describes an absolute gap, while a risk ratio and odds ratio describe relative comparisons. These measures answer related but not identical questions. Their interpretation is clearer when kept connected to the underlying group counts and denominators rather than treated as isolated statistics.

The record is also a reminder that a primary outcome and a secondary outcome should not automatically be treated as independent evidence. The 90-day mortality entry repeats the counts listed for the 28-day endpoint, and the registry reports no separate analysis. That pattern calls for careful reading of outcome definitions and analysis details rather than assuming that a second time point necessarily adds confirmation.

Finally, the sample-size illustrations show how planning requirements depend on the effect a study is intended to detect. Smaller target effects require more participants under the stated assumptions. Because the planning figures are based on the observed effect and are not the trial’s original design justification, they cannot establish whether the original study was adequately planned. The registry record does not report that original justification. Distinguishing a post hoc planning illustration from the trial’s own design assumptions is important for sound statistical interpretation.

18. Limitations

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

The registry record leaves important details about trial conduct and analysis unreported. It does not describe eligibility criteria in detail, recruitment setting, the randomization sequence method, allocation concealment, or which roles were masked. The placebo was described as identical in appearance and similarly administered, but further details about implementation are not reported in the registry record.

The analysis description is limited. No reported analyses are listed, and the registry does not specify the statistical test, analysis population, missing-data approach, or handling of protocol deviations. It does not report the original sample-size calculation, interim analyses, or the original statistical analysis plan. These gaps prevent a full evaluation of prespecification and robustness. They should not be treated as evidence that any particular procedure was absent or improperly conducted.

The secondary 90-day mortality entry has the same posted event counts as the 28-day primary outcome. The registry does not explain this, give a separate analysis, or provide information about deaths over time. This makes the secondary entry difficult to interpret as additional evidence. The registry also provides limited adverse-event detail: event definitions, severity, relatedness, and collection methods are not reported.

The posted group counts, 19 of 60 and 23 of 58 for primary mortality, leave uncertainty about the size and direction of the effect. The confidence interval spans zero. The registry does not state a clinical importance threshold or equivalence margin, so statistical results cannot be mapped to a prespecified standard of meaningful difference. Nor does the posted record provide information sufficient to assess generalizability to settings or populations beyond the trial participants.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Initiation of Hydrocortisone for the Treatment of Septic Shock — NCT02580240.
• Registry record last updated 2017-08-07; status last verified 2017-04.
• Results first posted 2017-08-07.
• 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

The registry describes NCT02580240, a completed randomized, parallel-group, quadruple-masked trial of hydrocortisone versus saline placebo for septic shock in adults. Enrollment was 118. The study start was recorded as 2015-09 and primary completion as 2016-09; the sponsor was Northern Jiangsu People's Hospital.

The primary outcome was death from any cause at 28 days after septic shock onset. The record posts 19 deaths among 60 placebo participants and 23 among 58 hydrocortisone participants. The risk-difference confidence interval includes zero, and the unadjusted p-value is 0.365. The registry lists all-cause mortality at 90 days as a secondary outcome with the same posted group counts.

The posted results leave substantial uncertainty about the treatment comparison. Further details about analysis populations, missing-data handling, multiplicity, the original design assumptions, and the interpretation of the repeated secondary counts are not reported in the registry record.