Neurosteroids as Novel Therapeutic Agents for Chronic Pain in OEF/OIF Veterans: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Neurosteroids as Novel Therapeutic Agents for Chronic Pain in OEF/OIF Veterans (NCT01898013), a randomized phase 2 study. The primary outcome is Change in Pain Intensity Rating (Visit 6-Baseline).

2. Clinical Question

The clinical question is about the difference between randomized groups, not simply whether either group’s score changed over time. Random assignment is intended to make the treatment groups comparable at the start, while the placebo group helps account for changes that might occur without active pregnenolone. The registry describes a one-week pain-diary period and a one-week placebo-only lead-in before the treatment period. The reported primary outcome compares baseline with Visit 6, after the treatment period described in the summary.

The registry reports an enrollment of 94 and describes a plan to assign 90 subjects equally between the two groups. The posted primary outcome data include 41 participants in the pregnenolone group and 42 in the placebo group. The record does not explain how those figures relate to enrollment or planned assignment, or define the population included in each analysis. The results therefore address the recorded analysis groups; they do not, by themselves, establish how every randomized participant contributed to the endpoint.

3. Trial Design

This was a phase 2, randomized, parallel-group trial of pregnenolone and placebo, listed as completed in the registry record. The sponsor was Durham VA Medical Center. The record gives a study start of 2013-09-13 and a primary completion date of 2017-04-03. It lists enrollment as 94. The registry summary describes the study as double-blind, while the structured masking entry is triple. The exact masking roles are not reported in the registry record, so those descriptions cannot be reconciled from the posted information.

The study summary describes pain diaries for one week, followed by a one-week placebo-only lead-in. It then describes random assignment to pregnenolone or placebo for four weeks, with 45 subjects planned for each group. The total study duration is described as six weeks, followed by two follow-up phone calls. Interviews and laboratory studies were planned at interview time points, including measurement of pregnenolone, allopregnanolone, and other neurosteroid metabolites. The record names gas chromatography / mass spectrometry and high performance liquid chromatography for those measurements.

The intervention description says pregnenolone was escalated on a fixed schedule up to 500mg/day. It gives 50mg PO, BID for the first treatment week, but the rest of the dosing schedule is incomplete in the registry record. The placebo was described as being administered in the same way as the active comparator. Further details about allocation concealment, sequence generation, adherence, treatment discontinuation, and the precise masking procedures are not reported in the registry record.

The primary endpoint is a continuous change score, reported as a least-squares mean for each group with standard errors. The primary outcome data list 41 participants for pregnenolone and 42 for placebo. These endpoint group counts differ from the planned assignment described in the summary, but the record does not explain the difference. It also does not state the analysis population or the handling of missing observations.

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.

Visit 3 (Randomization Visit)

Visit 4

Visit 5

Visit 6

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 Change in Pain Intensity Rating (Visit 6-Baseline), measured over Difference Scores (Visit 6-Baseline).

The primary endpoint is the change in pain intensity rating from baseline to Visit 6. Pain intensity was defined as the weekly mean of daily 24-hour average pain severity ratings, collected on an 11-point Likert scale ranging from 0, no pain, to 10, worst pain. The endpoint is the difference between the baseline and Visit 6 scores, rather than a single pain rating taken at one visit.

Averaging daily ratings into a weekly mean can describe pain over a period rather than relying on one potentially atypical day. Comparing the baseline and Visit 6 measurements focuses the analysis on change during the treatment period. Comparing that change between randomized groups is more informative about the trial question than looking at either group’s score in isolation, because both groups may change over time for reasons unrelated to the active intervention.

The posted group estimates are 4.11 for pregnenolone and 4.67 for placebo. The recalculated mean difference, defined as pregnenolone minus placebo, is -0.56. The trial’s outcome description identifies the scale direction, but does not clearly state the subtraction convention used to form the change score. Consequently, the between-group estimate can be described as favoring a lower change score in the pregnenolone group, without treating the score alone as a complete account of patients’ experience or making a clinical recommendation.

The endpoint is useful for evaluating the trial’s stated pain-intensity question, but it does not measure every aspect of chronic pain. Pain interference and other psychological or cognitive measures were listed as secondary outcomes. The primary endpoint also does not establish whether any observed difference persisted after the treatment and follow-up period described in the record.

7. Results Posted in the Registry

• Pregnenolone: mean 4.11 versus 4.67 on control; difference -0.56 (95% CI -1.05 to -0.07), standardized effect d = -0.50; z-test p = 0.024.

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.

Change in Pain Interference Scores (Visit 6-Baseline)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Pregnenolone: mean 1.84 versus 2.21 on control; difference -0.37 (95% CI -1.05 to 0.31), standardized effect d = -0.23; z-test p = 0.286.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregnenolone and the control. The interval gives the range of effects that remain compatible with the data.

Change in Beck Depression Inventory (Visit 6-Baseline)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Pregnenolone: mean 6.06 versus 6.26 on control; difference -0.20 (95% CI -0.45 to 0.05), standardized effect d = -0.34; z-test p = 0.119.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregnenolone and the control. The interval gives the range of effects that remain compatible with the data.

Change in Davidson Trauma Scale (Visit 6-Baseline)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Pregnenolone: mean 17.71 versus 15.04 on control; difference 2.67 (95% CI -20.57 to 25.91), standardized effect d = 0.05; z-test p = 0.822.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pregnenolone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover pain interference, depression, trauma symptoms, and cognitive tasks. Across the secondary comparisons with numerical results posted, the pattern is not a clear replication of the primary pain-intensity finding: the recalculated confidence intervals include zero, and the unadjusted p-values do not indicate a clear difference between groups. These results add context but do not establish that the groups were equivalent on those measures.

The registry lists five secondary outcome measures. Numerical comparison details are posted for pain interference, the Beck Depression Inventory, and the Davidson Trauma Scale. Numerical results for the Tower of London and Digit Sequence measures are not reported in the registry record. Their absence prevents a complete numerical assessment of the listed secondary outcomes.

Secondary endpoints can help show whether a primary result is accompanied by changes in related domains, but they are usually less persuasive when many outcomes are examined without a reported multiplicity plan. Each additional test creates another opportunity for a chance finding. The registry does not report whether the secondary analyses were prespecified in a detailed analysis plan, whether any multiplicity adjustment was used, or which secondary outcomes were intended to support confirmatory claims. The unadjusted secondary results should therefore be treated as exploratory context rather than as independent confirmation of the primary result.

The secondary findings also differ in the type of measure and the reported spread: for example, the Beck Depression Inventory is reported with standard deviations, while other measures list standard errors. Differences in scale and precision make simple comparisons of the numerical magnitudes across endpoints inappropriate. The secondary measures address distinct domains and should be interpreted on their own terms, with attention to the uncertainty and reporting gaps for each.

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

• Change in Pain Interference Scores (Visit 6-Baseline)
• Change in Beck Depression Inventory (Visit 6-Baseline)
• Change in Davidson Trauma Scale (Visit 6-Baseline)
• Change in Tower of London (Visit 6-Baseline)
• Change in Digit Sequence (Visit 6-Baseline)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s pain measure is represented by a numerical score, and the reported group summaries are means. The registry labels the group estimates as least-squares means and reports standard errors. A mean gives a central summary of the scores, while a standard error describes uncertainty in the estimated mean. A standard error is not the same thing as the spread of individual participant scores.

What does the mean difference represent?

The recalculated comparison subtracts the placebo mean from the pregnenolone mean. For the primary endpoint, the resulting estimate is -0.56. A negative value means the pregnenolone group’s reported mean change score is lower under that subtraction convention. The estimate is a contrast between group summaries; it is not a statement that every participant’s score changed by that amount. The trial’s own reported mixed-model estimate is also -0.56.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the estimate under the statistical model and its assumptions. It communicates uncertainty in a way that a single point estimate cannot. For the recalculated primary comparison, the interval excludes zero, which corresponds to the unadjusted p-value of 0.024 in this calculation. The registry does not give interval limits for the sponsor’s mixed-model result. A confidence interval does not show the probability that the true effect lies in the particular interval, and it does not decide whether a difference matters clinically.

Why distinguish the sponsor analysis from a recalculation?

The sponsor reports a mixed models analysis of final values, with a mean difference of -0.56 and p = 0.02. A mixed model uses a model-based approach rather than relying only on a direct comparison of the posted group summaries. The registry does not provide the model specification, covariates, or other details needed to reproduce that analysis. The recalculated result is an unadjusted calculation from posted summary statistics, not a substitute for the trial’s own analysis. Since the record does not identify a discrepancy, the sponsor’s analysis remains the primary reported inferential result.

Why can standard errors and standard deviations not be interchanged?

A standard deviation describes the variability of observations within a group. A standard error describes the uncertainty of an estimated quantity, such as a mean. They answer different questions. The primary endpoint and some secondary outcomes list standard errors, while the Beck Depression Inventory result lists standard deviations. Comparisons that rely on summary statistics must account for which quantity is reported. In the recalculation, some pooled variability values are approximated from the posted standard errors; such approximations should not be mistaken for participant-level data or the original model output.

Why can over-dispersion matter?

In general, over-dispersion means that data vary more than a chosen statistical model expects. When present, a model that assumes too little variation can make uncertainty appear smaller than it is. This is a general statistical concern, not a finding established by the registry record. The listed continuous outcomes are summarized with means and measures of spread, but the registry does not report diagnostic checks for distributional assumptions or over-dispersion. Those properties cannot be determined from the posted summaries alone.

What do p-values say?

A p-value measures how unusual data at least as extreme as those observed would be under a specified null model and its assumptions. The recalculated primary p-value is unadjusted, and the sponsor reports p = 0.02. Neither value is the probability that the null hypothesis is true, nor does either measure the size or clinical relevance of the estimated difference. Interpretation also depends on the analysis plan and the number of outcomes examined, details that are not fully reported in the registry record.

Why is randomization relevant?

In general, random assignment aims to balance measured and unmeasured characteristics across groups, reducing systematic differences that could otherwise complicate a treatment comparison. It does not guarantee identical groups, prevent missing data, or eliminate uncertainty. The registry identifies the allocation as randomized and the model as parallel. The sequence-generation and concealment procedures are not reported in the registry record, so the specific implementation cannot be evaluated from the posted information.

What does the analysis population affect?

The participants included in an analysis determine which observations contribute to its estimates. An analysis based on everyone assigned as planned can answer a different question from one based only on participants with observed endpoint data. The primary outcome counts are 41 and 42, whereas the summary describes 45 subjects planned for each group. The registry does not explain the difference or state whether the reported analysis follows an intention-to-treat, per-protocol, or other population definition. No population label should therefore be inferred from the available record.

11. Confidence Intervals and Precision

The recalculated primary comparison has a confidence interval that excludes zero. This indicates that, under the calculation’s assumptions, the posted data are not especially compatible with a zero difference at the interval’s confidence level. The interval is based on the posted summary statistics, rather than a confidence interval reported for the sponsor’s mixed-model analysis. The registry reports no interval limits for that analysis.

The point estimate of -0.56 is more informative when read alongside the interval than when read alone. The estimate identifies the center of the recalculated comparison, while the interval conveys a range of uncertainty around it. The interval does not guarantee that the true effect lies within its limits, and it does not establish whether differences of the sizes it permits would matter to participants. Statistical precision and clinical importance are separate questions.

Standard errors are reported for the primary group estimates, but participant-level data and the sponsor model details are not available in the registry record. The recalculated interval therefore depends on the summaries and assumptions used for that unadjusted calculation. It may not capture uncertainty related to missing outcomes, model choice, or other analysis decisions that are not documented.

The secondary endpoint intervals are less precise in relation to their estimates: the recalculated intervals include zero. That pattern is consistent with the secondary p-values and means those comparisons do not provide similarly clear evidence of a nonzero difference in these calculations. It does not prove that the groups are identical. A wide interval can leave substantial uncertainty, and the record does not report a prespecified clinical threshold against which to judge precision.

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 for continuous-outcome comparisons; they are not total event counts. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its starting point and then considers detecting the stated fraction of that effect. These are planning assumptions for the illustration, not reported assumptions from the trial’s original design.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is real. The 90% power column gives the corresponding estimate for a 90% chance. These are prospective design calculations, not measures of what happened in this completed trial. This is not observed power.

For the primary endpoint, planning for 100% of the observed effect gives 64 participants per arm for 80% power and 86 participants per arm for 90% power. Planning for 75% of the observed effect gives 114 participants per arm for 80% power and 152 participants per arm for 90% power. Planning for 50% of the observed effect gives 255 participants per arm for 80% power and 341 participants per arm for 90% power. The pattern illustrates a general design principle: smaller effects are harder to distinguish from random variation, so detecting them typically requires more participants.

These calculations use the observed effect as a planning reference, but an observed estimate can be uncertain and may not be the effect a future study should target. The registry does not report the trial’s original sample-size justification or its original power assumptions. The planning illustration should therefore not be read as evidence that the completed trial was designed around these participant counts, or as a retrospective assessment of its success.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.560; pooled standard deviation σ = 1.127.
2. n = 2 × (1.96 + 0.842)² × 1.127² / -0.560² = 63.6, rounded up to 64 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
delta <- -0.56                      # observed difference in means
sigma <- 1.12711693829549                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1898013)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 64 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 114 (80% power), 152 (90% power)
 50% of observed effect: n per arm = 255 (80% power), 341 (90% power)
power.t.test: 64.6 
Simulated power at n = 64 per arm: 0.794 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 mixed models analysis of final values. It gives a mean difference of -0.56 and p = 0.02. The recalculation from posted group summaries also gives a mean difference of -0.56, with an unadjusted p-value of 0.024 and a confidence interval excluding zero. The estimated direction and displayed effect size are aligned across these two presentations.

The sponsor’s analysis takes precedence as the trial’s own analysis. The recalculation is a simple unadjusted comparison based on summary statistics and is useful as a check on the posted group-level pattern. It cannot reproduce the mixed-model analysis because the registry does not report the model specification, participant-level observations, or all analysis details. The slight difference in displayed p-values is not, by itself, evidence that the estimates conflict; the registry reports the sponsor value to two decimal places and the recalculated value to three.

The sponsor’s primary result has no reported confidence interval in the registry record. The recalculated interval should not be attributed to the sponsor or described as the interval for the mixed model. The record does not identify a discrepancy between the reported and recalculated primary estimates, so there is no basis to prefer the recalculation over the sponsor result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and five secondary outcome measures. It also reports six outcome measures and six analyses. Testing several outcomes raises a multiplicity question: the more comparisons examined, the greater the chance that at least one result may appear notable by chance alone. This general concern does not invalidate the primary result, but it affects how much weight to place on unadjusted secondary findings and on any claims based on selecting among outcomes.

An adjustment for multiplicity, a testing hierarchy, or a prespecified strategy for interpreting the secondary outcomes is not reported in the registry record. The posted recalculated p-values are unadjusted. The sponsor’s primary analysis is reported with its p-value, but the record does not describe how that analysis fits into a broader multiplicity strategy. Therefore, the registry does not establish whether the primary result was protected from multiplicity in the original analysis plan.

The record reports endpoint group counts, but does not explain the analysis population, the number of missing endpoint observations, or how missing data were handled. It does not state whether participants were analyzed according to their randomized assignment, whether observations after treatment discontinuation were retained, or whether any imputation procedure was used. These details matter because the estimate can be influenced by which participants and observations enter an analysis, especially if missingness is related to symptoms or treatment experience.

The record also does not report an intention-to-treat or per-protocol designation for the primary analysis, the handling of protocol deviations, or the analysis population for secondary outcomes. Those features should not be inferred from the fact that allocation was randomized. Randomization describes assignment; it does not, on its own, define the set of participants included in the reported analysis.

Further details about interim analyses, stopping rules, and the statistical analysis plan are not reported in the registry record. Without them, the posted results can be described and compared, but the full prespecification and decision process cannot be assessed.

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 1% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events for the pregnenolone group as 0 affected among 45 at risk, and for the placebo group as 0 affected among 49 at risk. Deaths are listed as 0 in each group. The record does not list serious adverse-event terms.

For other adverse events, the registry lists 6 affected among 45 at risk in the pregnenolone group and 6 affected among 49 at risk in the placebo group. These figures describe the posted counts; they do not establish that the event types or their severity were the same between groups. The record does not provide the terms, timing, duration, or severity of the other adverse events in the information available for this summary.

The at-risk counts for the safety outcomes differ from the primary endpoint group counts, and the registry does not explain the relationship between those populations. No rates or comparisons are calculated. A zero serious-event count in the posted record does not show that serious harms are impossible or that all relevant safety outcomes were captured. These data should be read as the recorded event counts within the listed safety groups and reporting period, whose details are not reported in the registry record.

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

The primary result describes a difference in reported pain-intensity change scores between the pregnenolone and placebo groups. The recalculated estimate is -0.56, and the sponsor’s mixed-model analysis reports the same mean difference with p = 0.02. The recalculated confidence interval excludes zero. Together, these statistics indicate that the posted primary comparison favors a lower change score in the pregnenolone group under the stated subtraction convention, while still carrying uncertainty.

That statistical result does not, by itself, tell whether the difference was noticeable or important to participants. The registry does not report a threshold for a clinically meaningful change, patient-level response patterns, or a description of how the difference felt to participants. Group averages can also conceal variation: some people may have experienced a different course from the group mean.

The result does not establish that pregnenolone works or does not work in other settings, populations, or treatment durations. The registry describes a phase 2 trial in OEF/OIF Veterans with chronic low back pain, and the posted endpoint compares baseline with Visit 6. The record does not establish persistence beyond the period of measurement. It also does not provide the detail needed to evaluate the full analysis population, missing data, or all aspects of the statistical plan.

The secondary results do not offer clear statistical corroboration across the other measured domains. They should be interpreted cautiously because the record does not report a multiplicity strategy and because numerical results are not available for every listed secondary measure. The safety counts are descriptive and do not support a broad conclusion about risk.

Overall, the posted evidence is a trial-specific estimate with a statistically distinguishable primary comparison under the reported analyses, but important questions remain about precision, clinical importance, generalizability, and analysis details. It is evidence about the measured endpoint in this study, not individualized medical advice or a complete judgment about treatment.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through both its estimate and its uncertainty. The primary mean difference is -0.56, while the sponsor’s analysis and the recalculated summary-statistic comparison provide related but not identical inferential presentations. Separating the trial’s own mixed-model result from a simple recalculation helps readers understand what is reported by the investigators and what follows from the posted group summaries.

It also shows why statistical significance is not the same as clinical importance. A confidence interval excluding zero and a small unadjusted p-value address compatibility with a null difference under statistical assumptions. They do not establish the size of benefit that matters to participants, nor do they show that each participant experienced the average result. The record does not state a clinical threshold for interpreting the pain-score change.

The secondary outcomes highlight the role of multiplicity and selective interpretation. A primary comparison can be accompanied by several additional tests, and those tests need a clear plan if they are to support strong confirmatory conclusions. Here, the registry does not report a multiplicity adjustment or a detailed strategy for interpreting the family of outcomes. The secondary comparisons with posted numerical results do not provide a clear pattern of corroboration.

Finally, the gap between planned assignment and endpoint group counts underscores the importance of reporting analysis populations and missing-data handling. Randomization is central to trial design, but transparent accounting of who contributed data is also necessary for readers to judge the credibility and scope of the estimates. The registry record leaves those details unresolved.

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 registry record does not give the full dosing schedule for pregnenolone. It states that dosing escalated up to 500mg/day and describes 50mg PO, BID for the first treatment week, but the remaining schedule is incomplete. The exact protocol exposure therefore cannot be reconstructed from the posted description.

The record contains different descriptions of masking: the summary calls the trial double-blind, while the structured entry lists triple masking. It does not identify which people were masked or describe how masking was maintained. Allocation concealment and sequence-generation procedures are also not reported in the registry record.

The planned assignment in the summary is 45 subjects in each group, whereas the primary outcome summaries list 41 and 42. The safety at-risk counts are different again. The registry does not explain these counts, identify exclusions, or clarify whether the outcome and safety populations were defined differently. This limits assessment of participant flow and the possible effects of missing outcomes.

The sponsor reports a mixed-model analysis but does not provide its model specification, covariates, or a confidence interval. The registry does not report the original sample-size justification, a detailed statistical analysis plan, multiplicity handling, interim analyses, or a missing-data method. Numerical results for two listed secondary measures are not reported in the registry record.

The primary endpoint is a change score between baseline and Visit 6. The available description does not give a clinical-importance threshold or clarify the subtraction order used to define the within-participant change. The record also does not establish how long any difference persisted beyond the stated measurement period. These reporting limitations restrict interpretation of clinical meaning and durability.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Neurosteroids as Novel Therapeutic Agents for Chronic Pain in OEF/OIF Veterans — NCT01898013.
• Registry record last updated 2018-10-03; status last verified 2018-09.
• Results first posted 2018-10-03.
• 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

NCT01898013 is a completed phase 2 randomized parallel-group trial sponsored by Durham VA Medical Center. It compared pregnenolone with placebo for chronic low back pain in OEF/OIF Veterans. The registry lists enrollment as 94 and describes a planned allocation of 45 subjects to each group following pain diaries and a placebo-only lead-in.

The primary outcome was change in weekly mean 24-hour average pain severity from baseline to Visit 6, measured on an 11-point scale. The posted means were 4.11 for pregnenolone and 4.67 for placebo. The recalculated mean difference was -0.56, with an unadjusted p-value of 0.024; the sponsor’s mixed models analysis reported -0.56 and p = 0.02.

The record lists five secondary measures, but numerical results are not reported for all of them. It also leaves important details about masking, analysis populations, missing data, multiplicity, and the full dosing schedule unreported. The posted results describe the recorded endpoint comparisons and should be interpreted in light of those limits.